Case Study Research: Principles and Practices

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Case Study Research

Principles and Practices

Case Study Research: Principles and Practices aims to provide a gen-eral understanding of the case study method as well as specific tools forits successful implementation. These tools can be utilized in all fieldswhere the case study method is prominent, including anthropology,business, communications, economics, education, medicine, politicalscience, social work, and sociology. Topics covered include the defini-tion of a case study, the strengths and weaknesses of this distinctivemethod, strategies for choosing cases, an experimental template forunderstanding research design, and the role of singular observations incase study research. It is argued that a diversity of approaches – experi-mental, observational, qualitative, quantitative, ethnographic – may besuccessfully integrated into case study research. This book breaks downtraditional boundaries between qualitative and quantitative, experi-mental and nonexperimental, positivist and interpretivist.

John Gerring is currently associate professor of political science atBoston University. His books include Party Ideologies in America,1828–1996 (1998) and Social Science Methodology: A Criterial Frame-work (2001).

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Case Study Research


JOHN GERRINGBoston University

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CAMBRIDGE UNIVERSITY PRESS

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© John Gerring 2007

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For Liz, Kirk, Nicole, and Anthony,

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to pretend to have read Uncle John’s latest book.

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Historical knowledge and generalization (i.e., classificatory andnomothetic) knowledge . . . differ merely in the relative emphasisthey put upon the one or the other of the two essential and com-plementary directions of scientific research: in both cases we finda movement from concrete reality to abstract concepts and fromabstract concepts back to concrete reality – a ceaseless pulsationwhich keeps science alive and forging ahead.

– Florian Znaniecki (1934: 25)

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Contents

Acknowledgments page ix

1. The Conundrum of the Case Study 1

part i: thinking about case studies 15

2. What Is a Case Study? The Problem of Definition 17

3. What Is a Case Study Good For? Case Study versusLarge-N Cross-Case Analysis 37

part ii: doing case studies 65

4. Preliminaries 68

5. Techniques for Choosing Cases (with Jason Seawright) 86

6. Internal Validity: An Experimental Template (with RoseMcDermott) 151

7. Internal Validity: Process Tracing (with Craig Thomas) 172

Epilogue: Single-Outcome Studies 187

Glossary 211

References 219

Name Index 257

Subject Index 263

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Acknowledgments

I began thinking seriously about this project while conducting a workshopon case studies at Bremen University, sponsored by the Transformationsof the State Collaborative Research Center (CRC). I owe special thanksto my hosts in Bremen: Ingo Rohlfing, Peter Starke, and Dieter Wolf. Sub-sequently, the various parts of the project were presented at the ThirdCongress of the Working Group on Approaches and Methods in Com-parative Politics, Liege, Belgium; at the annual meetings of the Institutefor Qualitative Research (IQRM), Arizona State University; at the Cen-tro de Investigacion y Docencia Economicas (CIDE); and at the annualmeetings of the American Political Science Association. I am thankful forcomments and suggestions from participants at these gatherings.

The book evolved from a series of projects: articles in the AmericanPolitical Science Review, Comparative Political Studies, and InternationalSociology; chapters in the Oxford Handbook of Comparative Politics andthe Oxford Handbook of Political Methodology; and papers coauthoredwith Rose McDermott, Jason Seawright, and Craig Thomas.1 I am grate-ful to these coauthors, and to the publishers of these papers, for permissionto adapt these works for use in the present volume.

For detailed feedback on various drafts, I owe thanks to AndyBennett, Tom Burke, Melani Cammett, Kanchan Chandra, RenskeDoorenspleet, Colin Elman, Gary Goertz, Shareen Hertel, Staci Kaiser,Bernhard Kittel, Ned Lebow, Jack Levy, Evan Lieberman, Jim Mahoney,Ellen Mastenbroek, Devra Moehler, Howard Reiter, Kirsten Rodine,

1 See Gerring (2004b, 2006, 2007a, 2007b, 2007c); Gerring and McDermott (2005);Gerring and Thomas (2005); Seawright and Gerring (2005).

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x Acknowledgments

Ingo Rohlfing, Richard Snyder, Peter Starke, Craig Thomas, Lily Tsai,and David Woodruff. For clarification on various subjects, I am in debtto Bear Braumoeller, Patrick Johnston, Jason Seawright, Jas Sekhon, andPeter Spiegler.

This book also owes a large debt to a recent volume on the same subject,Case Studies and Theory Development by Alexander George and AndrewBennett – cited copiously in footnotes on the following pages. I like tothink of these two books as distinct, yet complementary, explorationsof an immensely complex subject. Anyone who, upon finishing this text,wishes further enlightenment should turn to George and Bennett.

My final acknowledgment is to the generations of scholars who havewritten on this subject, whose ideas I appropriate, misrepresent, or warpbeyond recognition. (In academic venues, the first is recognized as a cita-tion, the second is known as a reinterpretation, and the third is calledoriginal research.) The case study method has a long and largely neglectedhistory, beginning with Frederic Le Play (1806–1882) in France and theso-called Chicago School in the United States, including such luminaries asHerbert Blumer, Ernest W. Burgess, Everett C. Hughes, George HerbertMead, Robert Park, Robert Redfield, William I. Thomas, Louis Wirth,and Florian Znaniecki. Arguably, the case study was the first method ofsocial science. Depending upon one’s understanding of the method, it mayextend back to the earliest historical accounts or to mythic accounts ofpast events.2 Certainly, it was the dominant method of most of the socialscience disciplines in the nineteenth and early twentieth centuries.3 Amongcontemporary writers, the work of Donald Campbell, David Collier, andHarry Eckstein has been particularly influential on my own thinking aboutthese matters. It is a great pleasure to acknowledge my indebtedness tothese scholars.

2 Bernard (1928); Jocher (1928: 203).3 Glimpses of this early history can be found in Brooke (1970); Hamel (1993); and

in various studies conducted by members of the Chicago School (e.g., Bulmer 1984;Hammersley 1989; Smith and White 1921). A good survey of the concept as it has beenused in twentieth-century sociology can be found in Platt (1992). Dufour and Fortin(1992) provide an annotated bibliography, focusing mostly on sociology.


Case Study Research


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The Conundrum of the Case Study

There are two ways to learn how to build a house. One might studythe construction of many houses – perhaps a large subdivision or evenhundreds of thousands of houses. Or one might study the construction ofa particular house. The first approach is a cross-case method. The secondis a within-case or case study method. While both are concerned with thesame general subject – the building of houses – they follow different pathsto this goal.

The same could be said about social research. Researchers may chooseto observe lots of cases superficially, or a few cases more intensively. (Theymay of course do both, as recommended in this book. But there are usuallytrade-offs involved in this methodological choice.)

For anthropologists and sociologists, the key unit is often the socialgroup (family, ethnic group, village, religious group, etc.). For psycholo-gists, it is usually the individual. For economists, it may be the individual,the firm, or some larger agglomeration. For political scientists, the topicis often nation-states, regions, organizations, statutes, or elections.

In all these instances, the case study – of an individual, group, organi-zation or event – rests implicitly on the existence of a micro-macro link insocial behavior.1 It is a form of cross-level inference. Sometimes, in-depthknowledge of an individual example is more helpful than fleeting knowl-edge about a larger number of examples. We gain better understandingof the whole by focusing on a key part.

1 Alexander et al. (1987).

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2 Case Study Research

Two centuries after Frederic Le Play’s pioneering work, the variousdisciplines of the social sciences continue to produce a vast number ofcase studies, many of which have entered the pantheon of classic works.The case study research design occupies a central position in anthropol-ogy, archaeology, business, education, history, medicine, political science,psychology, social work, and sociology.2 Even in economics and politicaleconomy, fields not usually noted for their receptiveness to case-basedwork, there has been something of a renaissance. Recent studies of eco-nomic growth have turned to case studies of unusual countries such asBotswana, Korea, and Mauritius.3 Debates on the relationship betweentrade policy and growth have likewise combined cross-national regressionevidence with in-depth (quantitative and qualitative) case analysis.4 Workon ethnic politics and ethnic conflict has exploited within-country varia-tion or small-N cross-country comparisons.5 By the standard of praxis,

2 For examples, surveys of the case study method in various disciplines and subfields,see: anthropology/archeaology (Bernhard 2001; Steadman 2002); business, marketing,organizational behavior, public administration (Bailey 1992; Benbasat, Goldstein, andMead 1987; Bock 1962; Bonoma 1985; Jensen and Rodgers 2001); city and state poli-tics (Nicholson-Crotty and Meier 2002); comparative politics (Collier 1993; George andBennett 2005: Appendix; Hull 1999; Nissen 1998); education (Campoy 2004; Merriam1988); international political economy (Odell 2004; Lawrence, Devereaux, and Watkins2005); international relations (George and Bennett 2005: Appendix; Maoz 2002; Maozet al. 2004; Russett 1970); medicine, public health (Jenicek 2001; Keen and Packwood1995; Mays and Pope 1995; “Case Records from the Massachusetts General Hospital,”a regular feature in the New England Journal of Medicine; Vandenbroucke 2001); psy-chology (Brown and Lloyd 2001; Corsini 2004; Davidson and Costello 1969; Franklin,Allison, and Gorman 1997; Hersen and Barlow 1976; Kaarbo and Beasley 1999; Kennedy2005; Robinson 2001); social work (Lecroy 1998). For cross-disciplinary samplers, seeHamel (1993) and Yin (2004). For general discussion of the methodological properties ofthe case study (focused mostly on political science and sociology), see Brady and Collier(2004); Burawoy (1998); Campbell (1975/1988); Eckstein (1975); Feagin, Orum, andSjoberg (1991); George (1979); George and Bennett (2005); Gomm, Hammersley, andFoster (2000); Lijphart (1975); McKeown (1999); Platt (1992); Ragin (1987, 1997); Raginand Becker (1992); Stake (1995); Stoecker (1991); Van Evera (1997); Yin (1994); and thesymposia in Comparative Social Research 16 (1997). An annotated bibliography of works(primarily in sociology) can be found in Dufour and Fortin (1992).

3 Acemoglu, Johnson, and Robinson (2003); Chernoff and Warner (2002); Rodrik (2003).See also studies focused on particular firms or regions, e.g., Coase (1959, 2000) andLibecap (1989).

4 Srinivasan and Bhagwati (1999); Stiglitz (2002, 2005); Vreeland (2003).5 Abadie and Gardeazabal (2003); Chandra (2004); Miguel (2004); Posner (2004). For

additional examples of case-based work in political economy, see Abadie and Gardeazabal(2003); Alston (2005); Bates et al. (1998); Bevan, Collier, and Gunning (1999); Chang andGolden (in process); Fisman (2001); Huber (1996); Piore (1979); Rodrik (2003); Udry(2003); and Vreeland (2003).


The Conundrum of the Case Study 3

therefore, it would appear that the method of the case study is solidlyensconced, perhaps even thriving. Arguably, we are witnessing a move-ment in the social sciences away from a variable-centered approach tocausality and toward a case-based approach.6

Contributing to this movement is a heightened skepticism towardcross-case econometrics.7 It no longer seems self-evident that nonexper-imental data drawn from nation-states, cities, social movements, civilconflicts, or other complex phenomena should be treated in standardregression formats. The complaints are myriad, and oft-reviewed.8 Theyinclude: (a) the problem of arriving at an adequate specification of acausal model, given a plethora of plausible models, and the associatedproblem of modeling interactions among these covariates;9 (b) identifica-tion problems (which cannot always be corrected by instrumental variabletechniques);10 (c) the problem of “extreme” counterfactuals (i.e., extrap-olating or interpolating results from a general model where the extrapo-lations extend beyond the observable data points);11 (d) problems posedby influential cases;12 (e) the arbitrariness of standard significance tests;13

(f) the misleading precision of point estimates in the context of “curve-fitting” models;14 (g) the problem of finding an appropriate estimator and

6 This classic distinction has a long lineage. See, e.g., Abbott (1990); Abell (1987); Bendix(1963); Meehl (1954); Przeworski and Teune (1970: 8–9); Ragin (1987; 2004: 124); andZnaniecki (1934: 250–1).

7 Of the cross-country growth regression, a standard technique in economics and politicalscience, a recent authoritative review notes: “The weight borne by such studies is remark-able, particularly since so many economists profess to distrust them. The cross-sectional(or panel) assumption that the same model and parameter set applies to Austria andAngola is heroic; so too is the neglect of dynamics and path dependency implicit in theview that the data reflect stable steady-state relationships. There are huge cross-countrydifferences in the measurement of many of the variables used. Obviously importantidiosyncratic factors are ignored, and there is no indication of how long it takes for thecross-sectional relationship to be achieved. Nonetheless the attraction of simple general-izations has seduced most of the profession into taking their results seriously” (Winters,McCullock, and McKay 2004: 78).

8 For general discussion of the following points, see Achen (1986); Ebbinghaus (2005);Freedman (1991); Kittel (1999, 2005); Kittel and Winner (2005); Manski (1993);Winship and Morgan (1999); and Winship and Sobel (2004).

9 Achen (2002, 2005); Leamer (1983); Sala-i-Martin (1997).10 Bartels (1991); Bound, Jaeger, and Baker (1995); Diprete and Gangl (2004); Manski

(1993); Morgan (2002a, 2002b); Reiss (2003); Rodrik (2005); Staiger and Stock(1997).

11 King and Zeng (2004a, 2004b).12 Bollen and Jackman (1985).13 Gill (1999).14 Chatfield (1995).



modeling temporal autocorrelation in pooled time-series datasets;15 (h)the difficulty of identifying causal mechanisms;16 and, last but certainlynot least, (i) the ubiquitous problem of faulty data (measurement error).17

Many of the foregoing difficulties may be understood as the by-productof causal variables that offer limited variation through time, cases thatare extremely heterogeneous, and “treatments” that are correlated withmany possible confounders.

A second factor militating in favor of case-based analysis is the devel-opment of a series of alternatives to the standard linear/additive modelof cross-case analysis, thus establishing a more variegated set of tools tocapture the complexity of social behavior.18 Charles Ragin and associateshave explored ways of dealing with situations where different combina-tions of factors lead to the same set of outcomes, a set of techniquesknown as qualitative comparative analysis (QCA).19 Andrew Abbott hasworked out a method that maps causal sequences across cases, known asoptimal sequence matching.20 Bear Braumoeller, Gary Goertz, Jack Levy,and Harvey Starr have defended the importance of necessary-conditionarguments in the social sciences, and have shown how these argumentsmight be analyzed.21 James Fearon, Ned Lebow, Philip Tetlock, and oth-ers have explored the role of counterfactual thought experiments in theanalysis of individual case histories.22 Andrew Bennett, Colin Elman,and Alexander George have developed typological methods for analyz-ing cases.23 David Collier, Jack Goldstone, Peter Hall, James Mahoney,and Dietrich Rueschemeyer have worked to revitalize the comparativeand comparative-historical methods.24 And scores of researchers haveattacked the problem of how to convert the relevant details of a tempo-rally constructed narrative into standardized formats so that cases can bemeaningfully compared.25 While not all of these techniques are, strictly

15 Kittel (1999, 2005); Kittel and Winner (2005).16 George and Bennett (2005).17 Herrera and Kapur (2005).18 On this topic, see the landmark volume edited by Brady and Collier (2004).19 Drass and Ragin (1992); Hicks (1999: 69–73); Hicks et al. (1995); Ragin (1987, 2000);

several chapters by Ragin in Janoski and Hicks (1993); “Symposium: qualitative com-parative analysis (QCA)” (2004).

20 Abbott (2001); Abbott and Forrest (1986); Abbott and Tsay (2000).21 Braumoeller and Goertz (2000); Goertz (2003); Goertz and Levy (forthcoming); Goertz

and Starr (2003).22 Fearon (1991); Lebow (2000); Tetlock and Belkin (1996).23 Elman (2005); George and Bennett (2005: Chapter 11).24 Collier (1993); Collier and Mahon (1993); Collier and Mahoney (1996); Goldstone

(1997); Hall (2003); Mahoney (1999); Mahoney and Rueschemeyer (2003).25 Abbott (1992); Abell (1987, 2004); Buthe (2002); Griffin (1993).



speaking, case study techniques (they sometimes involve a rather largenumber of cases), they move us closer to a case-based understanding ofcausation insofar as they aim to preserve the texture and detail of indi-vidual cases, features that are often lost in large-N cross-case analyses.

A third factor inclining social scientists toward case-based methodsis the recent marriage of rational-choice tools with single-case analysis,sometimes referred to as an analytic narrative.26 Whether the technique isqualitative or quantitative, or some mix of both, scholars equipped witheconomic models are turning to case studies in order to test the theoreticalpredictions of a general model, to investigate causal mechanisms, and/orto explain the features of a key case.

Finally, epistemological shifts in recent decades have enhanced theattractiveness of the case study format. The “positivist” model of expla-nation, which informed work in the social sciences through most of thetwentieth century, tended to downplay the importance of causal mech-anisms in the analysis of causal relations. Famously, Milton Friedmanargued that the only criterion for evaluating a model was to be found inits accurate prediction of outcomes. The verisimilitude of the model, itsaccurate depiction of reality, was beside the point.27 In recent years, thisexplanatory trope has come under challenge from “realists,” who claim(among other things) that causal analysis should pay close attention tocausal mechanisms.28 Within political science and sociology, the identifi-cation of a specific mechanism – a causal pathway – has come to be seenas integral to causal analysis, regardless of whether the model in questionis formal or informal or whether the evidence is qualitative or quanti-tative.29 Given this newfound (or at least newly self-conscious) interestin mechanisms, it is hardly surprising that social scientists would turn tocase studies as a mode of causal investigation.

The Paradox

For all the reasons just stated, one might suppose that the case studyholds an honored place among methods currently taught and practiced

26 The term, attributed to Walter W. Stewart by Friedman and Schwartz (1963: xxi), waslater popularized by Bates et al. (1998), and has since been adopted more widely (e.g.,Rodrik 2003). See also Bueno de Mesquita (2000) and Levy (1990–91).

27 Friedman (1953). See also Hempel (1942) and Popper (1934/1968).28 Bhaskar (1978); Bunge (1997); Glennan (1992); Harre (1970); Leplin (1984); Little

(1998); Sayer (1992); Tooley (1988).29 Dessler (1991); Elster (1998); George and Bennett (2005); Hedstrom and Swedberg

(1998); Mahoney (2001); McAdam, Tarrow, and Tilly (2001); Tilly (2001).



in the social sciences. But this is far from evident. Indeed, the case studyresearch design is viewed by most methodologists with extreme circum-spection. A work that focuses its attention on a single example of abroader phenomenon is apt to be described as a “mere” case study, and isoften identified with loosely framed and nongeneralizable theories, biasedcase selection, informal and undisciplined research designs, weak empir-ical leverage (too many variables and too few cases), subjective conclu-sions, nonreplicability, and causal determinism.30 To some, the term casestudy is an ambiguous designation covering a multitude of “inferentialfelonies.”31

Arguably, many of the practitioners of this method are prone to invok-ing its name in vain – as an all-purpose excuse, a license to do whatevera researcher wishes to do with a chosen topic. Zeev Maoz notes,

There is a nearly complete lack of documentation of the approach to data collec-tion, data management, and data analysis and inference in case study research. Incontrast to other research strategies in political research where authors devote con-siderable time and effort to document the technical aspects of their research, oneoften gets the impression that the use of case study [sic] absolves the author fromany kind of methodological considerations. Case studies have become in manycases a synonym for free-form research where everything goes and the author doesnot feel compelled to spell out how he or she intends to do the research, why aspecific case or set of cases has been selected, which data are used and which areomitted, how data are processed and analyzed, and how inferences were derivedfrom the story presented. Yet, at the end of the story, we often find sweepinggeneralizations and “lessons” derived from this case.32

To say that one is conducting a case study sometimes seems to implythat normal methodological rules do not apply; that one has entered adifferent methodological or epistemological (perhaps even ontological)

30 Achen and Snidal (1989); Geddes (1990, 2003); Goldthorpe (1997); King, Keohane, andVerba (1994); Lieberson (1985: 107–15; 1992; 1994); Lijphart (1971: 683–4); Odell(2004); Sekhon (2004); Smelser (1973: 45, 57). It should be underlined that these writers,while critical of the case study format, are not necessarily opposed to case studies per se;that is to say, they should not be classified as opponents of the case study. More than anecho of current critiques can be found in earlier papers, e.g., Lazarsfeld and Robinson(1940) and Sarbin (1943, 1944). In psychology, Kratochwill (1978: 4–5) writes: “Casestudy methodology was typically characterized by numerous sources of uncontrolledvariation, inadequate description of independent, dependent variables, was generallydifficult to replicate. While this made case study methodology of little scientific value,it helped to generate hypotheses for subsequent research. . . .” See also Hersen, Barlow(1976: Chapter 1) and Meehl (1954).

31 Achen and Snidal (1989: 160).32 Maoz (2002: 164–5).



zone. As early as 1934, Willard Waller described the case study approachas an essentially artistic process.

Men who can produce good case studies, accurate and convincing pictures ofpeople and institutions, are essentially artists; they may not be learned men, andsometimes they are not even intelligent men, but they have imagination and knowhow to use words to convey truth.33

The product of a good case study is insight, and insight is

the unknown quantity which has eluded students of scientific method. That iswhy the really great men of sociology had no “method.” They had a method; itwas the search for insight. They went “by guess and by God,” but they found outthings.34

Decades later, a methods textbook describes case studies as a product of“the mother wit, common sense and imagination of person doing the casestudy. The investigator makes up his procedure as he goes along.”35

The quasi-mystical qualities associated with the case study persist tothis day. In the field of psychology, a gulf separates “scientists” engagedin cross-case research from “practitioners” engaged in clinical research,usually focused on individual cases.36 In the fields of political science andsociology, case study researchers are acknowledged to be on the soft side ofincreasingly hard disciplines. And across fields, the persisting case studyorientations of anthropology, education, law, social work, and variousother fields and subfields relegate them to the nonrigorous, nonsystematic,nonscientific, nonpositivist end of the academic spectrum.

Apparently, the methodological status of the case study is still highlysuspect. Even among its defenders there is confusion over the virtues andvices of this ambiguous research design. Practitioners continue to ply theirtrade but have difficulty articulating what it is they are doing, method-ologically speaking. The case study survives in a curious methodologicallimbo.

33 Waller (1934: 296–7).34 Ibid.35 Simon (1969: 267), quoted in Platt (1992: 18).36 Hersen and Barlow (1976: 21) write that in the 1960s, when this split developed, “clinical

procedures were largely judged as unproven, the prevailing naturalistic research wasunacceptable to most scientists concerned with precise definition of variables, cause-effectrelationships. On the other hand, the elegantly designed, scientifically rigorous groupcomparison design was seen as impractical, incapable of dealing with the complexities,idiosyncrasies of individuals by most clinicians.”



This leads to a paradox: although much of what we know about theempirical world has been generated by case studies, and case studies con-tinue to constitute a large proportion of the work generated by the socialscience disciplines (as demonstrated in the previous section), the casestudy method is generally unappreciated – arguably, because it is poorlyunderstood.

How can we make sense of the profound disjuncture between theacknowledged contributions of this genre to the various disciplines ofsocial science and its maligned status within these disciplines? If casestudies are methodologically flawed, why do they persist? Should they berehabilitated, or suppressed? How fruitful is this style of research?

Situating This Book

This book aims to provide a general understanding of the case study aswell as the tools and techniques necessary for its successful implementa-tion. The subtitle reflects my dual concerns with general principles as wellas with specific practices.

The first section explores some of the complexities embedded in thetopic. Chapter Two provides a definition of the case study and the log-ical entailments of this definition. A great deal flows from this defini-tion, so this is not a chapter that should be passed over quickly. ChapterThree addresses the methodological strengths and weaknesses of casestudy research, as contrasted with cross-case research. Case studies areuseful in some research contexts, but not in all. We need to do better inidentifying these different circumstances.

The second section of the book addresses the practical question of howone might go about constructing a case study. Chapter Four addresses pre-liminary issues. Chapter Five outlines a variety of strategies for choosingcases. Chapter Six proposes an experimental template for understandingcase study research design. Chapter Seven presents a rather different sortof approach called process tracing. An epilogue provides a short discus-sion of case studies whose purpose is to explain a single outcome, ratherthan a class of outcomes. (This is understood as a single-outcome study,to distinguish it from the garden-variety case study.) A glossary providesa lexicon of key terms.

A number of differences between the book in your hands and otherbooks exploring the same general topic should be signaled at the outset.First, unlike some texts, this one does not intend to provide a comprehen-sive review of methodological issues pertaining to social science research.



My intention, rather, is to hone in on those issues that pertain specificallyto case study research. Issues that apply equally to single-case and cross-case analysis are ignored, or are treated only in passing.37 Philosophy-of-science issues are almost entirely bypassed, except where they impingedirectly upon case study research.

Second, I focus on the role of case studies in facilitating causal anal-ysis. This is not intended to denigrate the interpretive case study or theessentially descriptive task of gathering evidence – for example, throughethnography, interviews, surveys, or primary and secondary accounts. IfI give these matters short shrift, it is only because they are well coveredby other authors.38

Third, rather than focusing on a single field or subfield of the social sci-ences, I take a broad, cross-disciplinary view of the topic. My conviction isthat the methodological issues entailed by the case study method are gen-eral, rather than field-specific. Moreover, by examining basic methodolog-ical issues in widely varying empirical contexts we sometimes gain insightsinto these issues that are not apparent from a narrower perspective. Exam-ples are drawn from all fields of the social sciences, and occasionally fromthe natural sciences. To be sure, the discussion betrays a pronouncedtilt toward my own discipline, political science, and toward two sub-fields where case studies have been particularly prominent – compara-tive politics and international relations. However, the arguments shouldbe equally applicable to anthropology, business, economics, history, law,medicine, organizational behavior, public health, social work, and socio-logy – indeed, to any field in the social sciences.

The reader should be aware that the examples chosen for discussion inthis book often privilege work that has come to be understood as classicor paradigmatic – that is, works that have elicited commentary from otherwriters. The inclusion of an exemplar should not be taken as an indicationthat I endorse the writer’s findings, or even her methodological choices.

37 I have assumed, for example, that the reader is aware of various injunctions such as thefollowing: (1) One’s use of sources – written, oral, or dataset – should be intelligent,taking into account possible biases and omissions; (2) whatever procedures the writerfollows (qualitative or quantitative, library work or field research) should be describedin enough detail to be replicable; (3) the author should consider plausible alternativesto the argument that she presents, those presented by the literature on a topic as wellas those that might suggest themselves to a knowledgeable reader. These standard-issuetopics are covered elsewhere, e.g., in Gerring (2001); King, Keohane, and Verba (1994);and in numerous handbooks devoted to qualitative or quantitative research.

38 See text citations in Chapter Four as well as the extensive bibliography at the end of thiswork.



It means only that a work serves as “a good example of X.” The pointof the example is thus to illustrate specific methodological issues, not toportray the state of research in a given field.

Indeed, many of my examples will be familiar to readers of othermethodological texts, where these examples have been chewed over. Thereplication of familiar examples should serve to enhance methodologicalunderstanding of difficult points, as recurrence to familiar cases enhancesclarity and consensus in the law. A case-based method rests on an in-depthknowledge of key cases, through which general points are elucidated andevaluated. It is altogether fitting, I might add, that a book on the casestudy method should assume a case-based heuristic.39

Foregrounding the Arguments

Although this purports to be a textbook on the case study, it is alsoinevitably an argument about what the case study should be. All methodstexts have this two-faced quality, even if the writer is not explicit abouther arguments. I wish to be as explicit as possible. What follows, there-fore, is a brief resume of larger arguments that circulate throughout thebook.

Qualitative and QuantitativeTraditionally, the case study has been associated with qualitative methodsof analysis. Indeed, the notion of a case study is sometimes employed asa broad rubric covering a host of nonquantitative approaches – ethno-graphic, clinical, anecdotal, participant-observation, process-tracing, his-torical, textual, field research, and so forth. I argue that this offhandusage should be understood as a methodological affinity, not a definitionalentailment. To study a single case intensively need not limit an investigatorto qualitative techniques. Granted, large-N cross-case analysis is alwaysquantitative, since there are (by construction) too many cases to handle ina qualitative way. Yet case study research may be either quant or qual, orsome combination of both, as emphasized in the following chapter and invarious examples sprinkled throughout the book. Moreover, there is noreason that case study work cannot accommodate formal mathematical

39 I do not mean to suggest that cases written for teaching purposes (e.g., at the HarvardBusiness School [Roberts 2002]), which are entirely descriptive (though they are intendedto allow students to reach specific conclusions), are similar to case studies written foranalytic purposes. This book is focused on the second, not the first.



models, which may help to elucidate the relevant parameters operativewithin a given case.40

Consider that the purpose of a statistical sample is to reveal elements ofa broader population. “The fundamental idea of statistics,” writes BradleyEfron, “is that useful information can be accrued from individual smallbits of data.”41 In this respect, the function of a sample is no differentfrom the function of a case study. If the within-case evidence drawn froma case study can be profitably addressed with quantitative techniques,these techniques must be assimilated into the case study method. Indeed,virtually all case studies produced in the social sciences today include somequantitative and qualitative components, and some of the most famouscase studies – including Middletown and Yankee City and the pioneeringfamily studies by Frederic Le Play – include a substantial portion of quan-titative analysis.42 The purely narrative case study, one with no numericalanalysis whatsoever, may not even exist. And I am quite sure that there isno purely quantitative case study, utterly devoid of prose.

Therefore, this book endeavors to speak to audiences who are versedin qualitative methods, as well as to those who are versed in quantitativemethods. This means finding a common vocabulary that will traverse theseestranged camps, and it means suggesting links across these two method-ological zones, wherever they may exist. This is more easily accomplishedin some situations than in others. I appeal to the reader’s forbearance indealing with contexts where our diverse lexicons do not match up neatlyor where qual/quant parallels are suggestive, but not exact.

Experimental and ObservationalThe virtues of the experimental method have been recognized by virtuallyevery methodological treatise since the time of Francis Bacon. However,not much is made of this fact in the social sciences, where the ambit of trulyexperimental methods has been quite limited (with the notable exceptionof the discipline of psychology). This is beginning to change.43 But thegeneral assumption remains that because experimental work is impossible

40 See, e.g., Houser and Freeman (2001) and Pahre (2005).41 Efron (1982: 341), quoted in King (1989: 12).42 Brooke (1970); Lynd and Lynd (1929/1956); Warner and Lunt (1941).43 For discussions of the experimental model of social science research, see Achen (1986);

Campbell (1988); Cook and Campbell (1979); Freedman (1991); Green and Gerber(2001); McDermott (2002); Winship and Morgan (1999); and Winship and Sobel (2004).The first person to advocate a quasi-experimental approach to case studies (to my knowl-edge) was Eckstein (1975). See also Lee (1989).



in most research settings, the experimental ideal is of little consequencefor practicing anthropologists, economists, political scientists, and soci-ologists. The pristine beauty of the true experiment is therefore regardedas a utopian ideal that can hardly be preserved if the real work of socialscience is to proceed.

I believe this dichotomization of research methods into experimentaland observational categories to be a mistake. Not only is the dichotomyambiguous, but it serves little purpose. There is no point in drawing asharp line between experimental and observational work, since both aim(or ought to aim) toward the same methodological ideals and both facethe same obstacles in this quest. Indeed, we gain purchase on the tasks ofresearch design – all research designs – by integrating the criteria employedin “experimental” work with the criteria applicable to “observational”work. The virtues of the experimental method extend to all methods, invarying degrees, and it is these degrees that ought to occupy the attentionof practitioners and methodologists.

I argue that many of the characteristic virtues and flaws of case studyresearch designs can be understood according to the degree to whichthey conform to, or deviate from, the true experiment. The experimentthus provides a useful template for discussion of methodological issues inobservational research, an ideal type against which to judge the utility ofall research designs. Often, the strongest defense of a case study is that itis quasi-experimental in nature. This is because the experimental ideal isoften better approximated within a small number of cases that are closelyrelated to one another, or by a single case observed over time, than by alarge sample of heterogeneous units.

Case Studies and Cross-Case StudiesA final argument concerns the traditional dichotomy between single-caseand cross-case evidence. Often, these modes of analysis are conceptualizedas being in opposition to each other. Work is classified as case study orlarge-N cross-case; researchers are lumped into one or the other school;journals adopt one or the other profile. It is not surprising that a degree ofskepticism – and occasionally, outright hostility – has crept into relationsbetween these disparate approaches to the empirical world.

However, rather than thinking of these methodological options asopponents, I suggest that we think of them as complements. Researchersmay do both and, arguably, must engage both styles of evidence. At thevery least, the process of case selection involves a consideration of thecross-case characteristics of a group of potential cases. Cases chosen for



case study analysis are identified by their status (extreme, deviant, and soforth) relative to an assumed population of cases. Thus, while we continueto categorize studies as predominantly case-oriented or variable-oriented,it is inappropriate to regard these two approaches as rival enterprises.44

My own experience in these matters is that reflection upon cross-casepatterns, far from being a hindrance to case study research, is, to thecontrary, a helpful tool. It helps one to formulate useful insights, to sepa-rate those that are limited in range from those that might travel to otherregions. And it certainly helps one to select cases and to explain the signif-icance of those cases (see Chapter Five). The more one knows about thepopulation, the more one knows about the cases, and vice versa. Hence,the virtue of cross-level research designs.45

By way of provocation, I shall insist there is no such thing as a casestudy, tout court. To conduct a case study implies that one has also con-ducted cross-case analysis, or at least thought about a broader set ofcases. Otherwise, it is impossible for an author to answer the definingquestion of all case study research: what is this a case of? So framed,this book should be of interest to scholars in both the “cross-case” and“case study” camps. Indeed, my hope is that this book will contribute tobreaking down the rather artificial boundaries that have separated thesegenres within the social sciences. Properly constituted, there is no reasonthat case study results cannot be synthesized with results gained fromcross-case analysis, and vice versa.

44 This distinction is drawn from Ragin (1987; 2004: 124). It is worth noting that Ragin’sdistinctive method (QCA) is also designed to overcome this traditional dichotomy.

45 Achen and Shively (1995); Berg-Schlosser and De Meur (1997); Moaz and Mor (1999);Wong (2002). For a skeptical view of cross-level research, see Lieberson (1985: 107–15).


14


part i

THINKING ABOUT CASE STUDIES

Narrow debates pertaining to specific methods can often be resolved by anappeal to context (which method is appropriately applied in setting A?),or by an investigation of the mathematical properties underlying differentstatistical methods (e.g., which technique of modeling serial autocorrela-tion is consistent with our understanding of a phenomenon and with theevidence at hand?). Broader methodological debates, however, are alwaysand necessarily about concepts. How should we define key terms (e.g.,“case,” “causation,” “process-tracing”)? What is the most useful way tocarve up the lexical terrain?1

It will be seen that these questions of definition are inextricable fromthe broader questions of social science methodology. For it is with thesekey terms that we make sense of the subject matter. Thus, while the firstpart of the book is prefatory to the practical advice offered in Part Two,it is certainly not incidental. It is impossible to conduct case studies with-out also conceptualizing the case study and its place in the toolbox ofsocial research. In thinking this matter through, a degree of abstractionis inevitable. I have endeavored to leaven the generalities with specificexamples, wherever possible.

Chapter Two asks what a case study is, and how it might be differen-tiated from other styles of research. This chapter is definitional. It dealswith the various meanings that have been attached to, or are implied by,the case study research design.

1 For discussion of concept formation in the social sciences see Adcock (2005); Collier andMahon (1993); Gerring (2001: Chapters 3–4); and Sartori (1984).

15


16 I. Thinking about Case Studies

Building on this scaffolding, Chapter Three inquires into the strengthsand weaknesses of the case study method, as contrasted with cross-casemethods. Under what conditions is a case study approach most useful,most revealing, or most suspect?


2

What Is a Case Study?

The Problem of Definition

The key term of this book is, admittedly, a definitional morass. To referto a work as a “case study” might mean: (a) that its method is quali-tative, small-N,1 (b) that the research is holistic, thick (a more or lesscomprehensive examination of a phenomenon),2 (c) that it utilizes aparticular type of evidence (e.g., ethnographic, clinical, nonexperimen-tal, non-survey-based, participant-observation, process-tracing, histori-cal, textual, or field research),3 (d) that its method of evidence gatheringis naturalistic (a “real-life context”),4 (e) that the topic is diffuse (caseand context are difficult to distinguish),5 (f) that it employs triangulation(“multiple sources of evidence”),6 (g) that the research investigates theproperties of a single observation,7 or (h) that the research investigatesthe properties of a single phenomenon, instance, or example.8

Evidently, researchers have many things in mind when they talk aboutcase study research. Confusion is compounded by the existence of a

1 Eckstein (1975); George and Bennett (2005); Lijphart (1975); Orum, Feagin, and Sjoberg(1991: 2); Van Evera (1997: 50); Yin (1994).

2 Goode and Hart (1952: 331; quoted in Mitchell 1983: 191); Queen (1928: 226); Ragin(1987, 1997); Stoecker (1991: 97); Verschuren (2003).

3 George and Bennett (2005); Hamel (1993); Hammersley and Gomm (2000); Yin (1994).4 Yin (2003: 13).5 Yin (1994: 123).6 Ibid.7 Campbell and Stanley (1963: 7); Eckstein (1975: 85).8 This is probably the most common understanding of the term. George and Bennett (2005:

17), for example, define a case as “an instance of a class of events.” (Note that elsewherein the same chapter they infer that the analysis of that instance will be small-N, i.e.,qualitative.) See also Odell (2001: 162) and Thies (2002: 353).

17



large number of near-synonyms – single unit, single subject, single case,N=1, case-based, case-control, case history, case method, case record,case work, within-case, clinical research, and so forth.9 As a result of thisprofusion of terms and meanings, proponents and opponents of the casestudy marshal a wide range of arguments but do not seem any closer toagreement than when this debate was first broached several decades ago.Jennifer Platt notes that “much case study theorizing has been conceptu-ally confused, because too many different themes have been packed intothe idea ‘case study.’”10

How, then, should the case study be understood? The first six optionsenumerated above (a–f) seem inappropriate as general definitions ofthe topic, since each implies a substantial shift in meaning relative toestablished usage. One cannot substitute case study for qualitative, ethno-graphic, process-tracing, holistic, naturalistic, diffuse, or triangulationwithout feeling that something has been lost in translation. These termsare perhaps better understood as describing certain kinds of case studies,not the topic at large. A seventh option, (g), equates the case study withthe study of a single observation, the N = 1 research design. This islogically impossible, as I will argue. The eighth option, (h), centeringon phenomenon, instance, or example as the key term, is correct as faras it goes but also ambiguous. Imagine asking someone, “What is yourinstance?” or “What is your phenomenon?” A case study presupposes arelatively bounded phenomenon, an implication that none of these termscaptures.

Can this concept be reconstructed in a clearer, more productivefashion? I begin this chapter by stipulating a series of definitions. I thenpresent a typology of research designs, understood according to the pat-terns of spatial and temporal evidence that they draw upon. A final sectionaddresses a central definitional question, namely, whether case studiesshould be understood as exclusively “small-N” analyses.

9 Davidson and Costello (1969); Franklin, Allison, and Gorman (1997); Hersen andBarlow (1976); Kazdin (1982); Kratochwill (1978).

10 Platt (1992: 48). Elsewhere in this perceptive article, Platt (1992: 37) comments: “thediversity of the themes which have been associated with the term, and the vagueness ofsome of the discussion, causes some difficulty. . . . In practice, ‘case study method’ in itsheyday [in the interwar years] seems to have meant some permutation of the followingcomponents: life history data collected by any means, personal documents, unstructuredinterview data of any kind, the close study of one or a small number of cases whetheror not any attempt was made to generalize from them, any attempt at holistic study, andnon-quantitative data analysis. These components have neither a necessary logical nor aregular empirical connection with each other.”


What Is a Case Study? 19

Definitions

For purposes of methodological discussion, it is essential to develop avocabulary that is consistent and clear. In arriving at definitions for keyterms, I rely on ordinary usage (within the language region of socialscience) as much as possible. However, because ordinary usage is oftenambiguous, encompassing a range of meanings for a given term (as wehave seen above for “case”), some concept reconstruction is unavoidable.At the end of this discussion, I hope it will be clear why this particular wayof defining terms might be useful, at least for methodological purposes.11

Case connotes a spatially delimited phenomenon (a unit) observed at asingle point in time or over some period of time. It comprises the type ofphenomenon that an inference attempts to explain. Thus, in a study thatattempts to elucidate certain features of nation-states, cases are comprisedof nation-states (across some temporal frame); in a study that attemptsto explain the behavior of individuals, cases are comprised of individuals,and so forth. Each case may provide a single observation or multiple(within-case) observations.

For students of political science, the archetypal case is the dominantpolitical unit of our time, the nation-state. However, this is a matter ofconvention. The study of smaller social and political units (regions, cities,villages, communities, social groups, families) or specific institutions(political parties, interest groups, businesses) is equally common in manysocial science disciplines.12 In psychology, medicine, and social work thenotion of a case study is usually linked to clinical research, where individ-uals are the preferred units of analysis.13 Whatever one’s chosen unit, themethodological issues attached to the case study have nothing to do withthe size of the cases. A case may be created out of any phenomenon so longas it has identifiable boundaries and comprises the primary object of aninference.

Note that the spatial boundaries of a case are often more apparentthan its temporal boundaries. We know, more or less, where a countrybegins and ends, while we may have difficulty explaining when a country

11 In the following analysis, I take a “minimal” approach to definition (Gerring 2001:Chapter 4; Gerring and Barresi 2003). Scholars embedded in a particular research settingmay choose somewhat different terms and meanings.

12 For discussion of subnational studies in political science, see Snyder (2001).13 Corsini (2004); Davidson and Costello (1969); Hersen and Barlow (1976); Franklin,

Allison, and Gorman (1997); Robinson (2001). For discussion of the meaning of theterm “case study,” see Benbasat, Goldstein, and Mead (1987: 371); Cunningham (1997);Merriam (1988); and Verschuren (2003).



begins and ends. Yet some temporal boundaries must be assumed. Thisis particularly important when cases consist of discrete events – crises,revolutions, legislative acts, and so forth – within a single unit. Occasion-ally, the temporal boundaries of a case are more obvious than its spatialboundaries. This is true when the phenomena under study are eventful butthe unit undergoing the event is amorphous. For example, if one is study-ing terrorist attacks it may not be clear how the spatial unit of analysisshould be understood, but the events themselves may be well bounded.

A case study may be understood as the intensive study of a single casewhere the purpose of that study is – at least in part – to shed light on alarger class of cases (a population). Case study research may incorporateseveral cases, that is, multiple case studies. However, at a certain point itwill no longer be possible to investigate those cases intensively. At the pointwhere the emphasis of a study shifts from the individual case to a sampleof cases, we shall say that a study is cross-case. Evidently, the distinctionbetween case study and cross-case study is a matter of degree. The fewercases there are, and the more intensively they are studied, the more a workmerits the appellation “case study.” Even so, this proves to be a usefuldistinction, and much follows from it. Indeed, the entire book rests uponit. All empirical work may be classified as either case study (comprisingone or a few cases) or cross-case study (comprising many cases).

An additional implication of the term “case study” is that the unit(s)under special focus is not perfectly representative of the population, or isat least questionable. Unit homogeneity across the sample and the popula-tion is not assured. If, for example, one is studying a single H20 molecule,it may be reasonable to assume that the behavior of that molecule is iden-tical to that of all other H20 molecules. Under the circumstances, onewould not refer to such an investigation as a “case study,” regardless ofhow intensive the investigation of that single molecule might be. In socialscience settings one rarely faces phenomena of such consistency, so thisis not an issue of great practical significance. Nonetheless, intrinsic to theconcept is an element of doubt about the bias that may be contained in asample of one or several.

A few additional terms may now be formally defined.An observation is the most basic element of any empirical endeavor.

Conventionally, the number of observations in an analysis is referred towith the letter N. (Confusingly, N may also be used to designate the num-ber of cases in a study, a usage that is usually clear from context.) A singleobservation may be understood as containing several dimensions, eachof which may be measured (across disparate observations) as a variable.



Where the proposition is causal, these may be subdivided into depen-dent (Y) and independent (X) variables. The dependent variable refers tothe outcome of an investigation. The independent variable refers to theexplanatory (causal) factor, that which the outcome is supposedly depen-dent on.

A case may consist of a single observation (N=1). This would be true,for example, in a cross-sectional analysis of multiple cases. In a case study,however, the case under study always provides more than one observation.These may be constructed diachronically (by observing the case or somesubset of within-case units over time) or synchronically (by observingwithin-case variation at a single point in time), as discussed below.

This is a clue to the fact that case studies and cross-case studies usuallyoperate at different levels of analysis. The case study is typically focusedon within-case variation (if there is a cross-case component, it is proba-bly secondary in importance to the within-case evidence). The cross-casestudy, as the name suggests, is typically focused on cross-case variation (ifthere is also within-case variation, it is probably secondary in importanceto the cross-case evidence). They have the same object in view – the expla-nation of a population of cases – but they go about this task differently.

A sample consists of whatever cases are subjected to formal analysis;they are the immediate subject of a study or case study. (Confusingly,the term “sample” may also refer to the observations under study. Butat present, we treat the sample as consisting of cases.) In a case study,the sample is small, by definition, consisting of the single case or handfulof cases that the researcher has under her lens. Usually, however, whenone uses the term “sample” one is implying that the number of casesis large. Thus, “sample-based work” will be understood as referring tolarge-N cross-case methods – the opposite of case study work. To reiterate,the feature distinguishing the case study format from a sample-based (or“cross-case”) research design is the number of cases falling within thesample – one or a few versus many – and the corresponding thoroughnesswith which each case is studied. Case studies, like large-N samples, seek torepresent, in all ways relevant to the proposition at hand, a population ofcases. A series of case studies might therefore be referred to as a sample ifthey are relatively brief and relatively numerous; it is a matter of emphasisand of degree. The more case studies one has, the less intensively each oneis studied, and the more confident one is in their representativeness (ofsome broader population), the more likely one is to describe them as asample rather than as a series of case studies. For practical reasons –unless, that is, a study is extraordinarily long – the case study research



format is usually limited to a dozen cases or fewer. A single case is notunusual.

Granted, in some circumstances a single study may combine the twoelements – an intensive case study and a more superficial analysis con-ducted on a larger sample. These additional cases are often brought intothe analysis in a peripheral way – typically, in an introductory or con-cluding section of the paper or the book. Often, these peripheral cases aresurveyed through a quick reading of the secondary literature or througha statistical analysis. Sometimes, the status of these informal cases is leftimplicit (they are not theorized as part of the formal research design).This may be warranted in circumstances where the relevant compari-son or contrast between the formal case(s) under intensive study and theperipheral cases is obvious. Thus, studies of American exceptionalism, inenumerating features of the American experience, often assume that theUnited States is different from European countries in relevant respects.14

In this situation, the additional cases – the UK, France, Germany, andso on – provide the necessary background for whatever arguments arebeing made about America. They are present, in the sense that they carryan important burden in the analysis, but perhaps they are not formallyaccounted for in the author’s research design. For our purposes, what issignificant is that most works combine case study and cross-case studycomponents, whether or not the latter are explicit. Methodologically,these approaches are distinct, even though they may be integrated intoa single work. (Indeed, this is a good way of approaching many subjects.)

Continuing with our review of key terms, the sample of cases (largeor small) rests within a population of cases to which a given propositionrefers. The population of an inference is thus equivalent to the breadthor scope of a proposition. (I use the terms proposition, hypothesis, infer-ence, and argument interchangeably.) Note that most samples are notexhaustive; hence the use of the term “sample,” referring to samplingfrom a larger population. Occasionally, however, the sample equals thepopulation of an inference; all potential cases are studied.

For those familiar with the rectangular form of a dataset, it may be help-ful to conceptualize observations as rows, variables as columns, and casesas either groups of observations or individual observations. Several pos-sibilities are illustrated in the tables presented here: two cases (Table 2.1),multiple cross-sectional cases (Table 2.2), and time-series cross-sectionalcases (Table 2.3).

14 Amenta (1991).


table 2.1. Case study dataset with two cases

X1 X2 YObs 1.1Obs 1.2Obs 1.3Obs 1.4Obs 1.5Obs 1.6Obs 1.7Obs 1.8Obs 1.9

Obs 1.10Case 1Obs 1.11Obs 1.12Obs 1.13Obs 1.14Obs 1.15Obs 1.16Obs 1.17Obs 1.18Obs 1.19Obs 1.20 Population Sample

Obs 2.1Obs 2.2Obs 2.3Obs 2.4Obs 2.5Obs 2.6Obs 2.7Obs 2.8Obs 2.9

Obs 2.10Case 2Obs 2.11Obs 2.12Obs 2.13Obs 2.14Obs 2.15Obs 2.16Obs 2.17Obs 2.18Obs 2.19Obs 2.20

Population = 1; Sample = 1; Cases = 2; Observations (N) = 40; Variables = 3.

23


table 2.2. Cross-case cross-sectional dataset with forty cases

X1 X2 YCase 1 Obs 1Case 2 Obs 2Case 3 Obs 3Case 4 Obs 4Case 5 Obs 5Case 6 Obs 6Case 7 Obs 7Case 8 Obs 8Case 9 Obs 9

Case 10 Obs 10Case 11 Obs 11Case 12 Obs 12Case 13 Obs 13Case 14 Obs 14Case 15 Obs 15Case 16 Obs 16Case 17 Obs 17Case 18 Obs 18Case 19 Obs 19Case 20 Obs 20Population SampleCase 21 Obs 21Case 22 Obs 22Case 23 Obs 23Case 24 Obs 24Case 25 Obs 25Case 26 Obs 26Case 27 Obs 27Case 28 Obs 28Case 29 Obs 29Case 30 Obs 30Case 31 Obs 31Case 32 Obs 32Case 33 Obs 33Case 34 Obs 34Case 35 Obs 35Case 36 Obs 36Case 37 Obs 37Case 38 Obs 38Case 39 Obs 39Case 40 Obs 40

Population = 1; Sample = 1; Cases = 40; Observations (N) = 40; Variables = 3.

24


table 2.3. Time-series cross-sectional dataset

X1 X2 Y Obs 1.1 (T1) Obs 1.2 (T2)

Case 1 Obs 1.3 (T3) Obs 1.4 (T4) Obs 1.5 (T5) Obs 2.1 (T1) Obs 2.2 (T2)



Case 4 Obs 4.3 (T3) Obs 4.4 (T4) Obs 4.5 (T5) Population

Sample Obs 5.1 (T1) Obs 5.2 (T2)




Case 8 Obs 8.3 (T3) Obs 8.4 (T4) Obs 8.5 (T5)

Population = 1; Sample = 1; Cases = 8; Observations (N) = 40; Time (T) = 1–5;Variables = 3.

25



It must be appreciated that all these terms are definable only by ref-erence to a particular proposition and a corresponding research design.A country may function as a case, an observation, or a population. It alldepends upon what one is arguing. In a typical cross-country time-seriesregression analysis, cases are countries and observations are country-years.15 However, shifts in the level of analysis of a proposition necessarilychange the referential meaning of all terms in the semantic field. If onemoves down one level of analysis, the new population lies within the oldpopulation, the new sample within the old sample, and so forth. Popula-tion, case, and observation are nested within each other. Since most socialscience research occurs at several levels of analysis, these terms are gener-ally in flux. Nonetheless, they have distinct meanings within the contextof a single proposition and its associated research design.

Consider a survey-based analysis of respondents within a single coun-try, under several scenarios. Under the first scenario, the proposition ofinterest pertains to individual-level behavior. It is about how individualsbehave. As such, cases are defined as individuals, and this is properly clas-sified as a cross-case study. Now, let us suppose that the researcher wishesto use this same survey-level data drawn from a single country to eluci-date an inference pertaining to countries, rather than to individuals. Underthis scenario, each poll respondent constitutes a within-case observation.If there is only one country, or a few countries, under investigation –and the inference, as before, pertains to multiple countries – then thisstudy is properly classified as a case study. If many countries are understudy (with or without individual-level data), then it is properly classifiedas a cross-case study. Again, the key questions are (a) how many cases arestudied and (b) how intensively are they studied – with the understandingthat a “case” embodies the unit of concern in the central inference.

To complicate matters further, the status of a work may change as it isdigested and appropriated by a community of scholars. A meta-analysisis a systematic attempt to integrate the results of individual studies into aquantitative analysis, pooling individual cases drawn from each study intoa single dataset (with various weightings and restrictions). The ubiquitousliterature review or case study survey aims at the same objective in a lesssynoptic fashion. Both statistical meta-analyses and narrative literaturereviews assimilate a series of studies, treating them as case studies insome larger project – whether or not this was the intention of the originalauthors.16

15 See, e.g., Przeworski et al. (2000).16 Lipsey and Wilson (2001); Lucas (1974).



A Typology of Covariational Research Designs

In order to better understand what a case study is, one must comprehendwhat it is not. The distinctiveness of the case study may be clarified byplacing it within a broader set of methodological options. Here, I shallclassify research designs according to (a) the number of cases that theyencompass (one, several, or many), (b) the kind of X/Y variation that theyexploit (spatial or temporal), and (c) the location of that variation (cross-case or within-case). This produces a typology with ten possible cells, asdepicted in Table 2.4.

Variations on the case study format occupy five of these ten cells, desig-nated by the shaded regions in Table 2.4. Type 2 represents variation in asingle case over time (diachronic analysis). Type 3 represents within-casevariation at a single point in time (synchronic analysis). Type 4 combinessynchronic and diachronic analysis, and is perhaps the most commonapproach in case study work. Thus, Robert Putnam’s classic study ofItaly, Making Democracy Work, exploits variation across regions andover time in order to test the causal role of social capital.17

It is common to combine several cases in a single study. If the cases arecomprised of large territorial units, then this combination may be referredto as the “comparative” method (if the variation of interest is primarilysynchronic) or the “comparative-historical” method (if the variation ofinterest is both synchronic and diachronic).18 It should be pointed outthat these terms are used primarily within the subfield of comparativepolitics. Other terms, such as “most-similar” and “most-different,” maybe used as well. Thus, while a case is always singular, a case study workor research design often refers to a study that includes several cases.

The larger point is that the evidentiary basis upon which case stud-ies rely is plural, not singular. Indeed, there are five possible styles ofcovariational evidence in a case study. Usually, they are intermingled –different sorts of analysis will be employed at different stages of the anal-ysis – so that it is often difficult to categorize a study as falling neatly intoa single cell in Table 2.4.

The bottom half of Table 2.4 lays out various cross-case researchdesigns, where the most important element of the empirical analysisinvolves comparisons across many cases (more than a handful). Cross-case

17 Putnam (1993).18 On the comparative method see Collier (1993); Lijphart (1971, 1975); Przeworski and

Teune (1970); Richter (1969); and Smelser (1976). On the comparative-historical methodsee Mahoney and Rueschemeyer (2003). On the history of the comparative method, aterm that harkens back to Bryce (1921), see Lasswell (1931).



table 2.4. Research designs: A covariational typology

Cases Spatial Variation Temporal Variation

No Yes

None 1. [Logically impossible] One

Within-case 3. Single-case study (synchronic)

4. Single-case study (synchronic + diachronic)

Several Cross-case & within-case 5. Comparative method 6. Comparative-historical

Cross-case 7. Cross-sectional 8. Time-series cross-sectional

Many

Note: Shaded cells are case study research designs.

Cross-case & within-case 9. Hierarchical 10. Hierarchical time-series

2. Single-case study (diachronic)

analysis without any explicit temporal component (type 7) is usually clas-sified as cross-sectional, even though a temporal component is simulatedwith independent variables that are assumed to precede the dependentvariable. An example was illustrated in Table 2.2. When an explicit tem-poral component is included, we often refer to the analysis as time-seriescross-sectional (TSCS) or pooled time-series (type 8). This format wasillustrated in Table 2.3. When one examines across-case and within-casevariation in the same research design, one is said to be employing a hier-archical model (type 9). Finally, when all forms of covariation are enlistedin a single research design, the resulting method may be described as ahierarchical time-series design (type 10).19

It bears repeating that I have listed the methods most commonly iden-tified with these research designs not with the intention of distinguishinglabels but rather with the intention of illustrating various types of causal

19 It will be noted that, like most case studies, hierarchical models involve a movement acrosslevels of analysis. However, while a case study moves down from the primary level ofanalysis (to within-case cases), a hierarchical model moves up. Thus, if classrooms arethe primary unit of analysis in a study, one might employ a hierarchical model to controlfor the effects of larger cases – schools, districts, regions, and so forth. But one would notemploy individual students as cases in such an analysis (not, that is, without changingthe unit of analysis for the entire study).



evidence. The classification of a research design always depends uponthe particular proposition that a researcher intends to prove. Potentially,each of the foregoing cross-case methods might also be employed in thecapacity of a case study. (That is, a case study may enlist cross-sectional,time-series cross-sectional, hierarchical, or hierarchical time-series tech-niques.) It all depends upon the proposition in question (i.e., what sortof phenomena it is about, and hence what sort of phenomena constitutes“cases”) and on the degree of analytic focus devoted to the individualcases.

The N Question

Traditionally, the case study has been identified with qualitative methodsand cross-case analysis with quantitative methods. This is how FranklinGiddings put the matter in his 1924 textbook, in which he contrasted twofundamentally different procedures:

In the one we follow the distribution of a particular trait, quality, habit or otherphenomenon as far as we can. In the other we ascertain as completely as wecan the number and variety of traits, qualities, habits, or what not, combined ina particular instance. The first of these procedures has long been known as thestatistical method. . . . The second procedure has almost as long been known asthe case method.20

In the intervening decades, this disjunction has become ever more en-sconced: a contrast between “stats” and “cases,” “quant” and “qual.”Those who work with numbers are apt to distrust case study methods,while those who work with narratives are likely to be favorably disposed.

I believe that this distinction is not intrinsic, that is, definitional. Whatdistinguishes the case study method from all other methods is its relianceon evidence drawn from a single case and its attempt, at the same time,to illuminate features of a broader set of cases. It follows from this thatthe number of observations (N) employed by a case study may be eithersmall or large, and consequently may be evaluated in a qualitative orquantitative fashion.21

20 Giddings (1924: 94). See also Meehl (1954); Rice (1928: Chapter 1); and Stouffer (1941:349).

21 This section explains and elaborates on a theme first articulated by Lundberg (1941),followed by Campbell (1975/1988) – itself a revision of Campbell’s earlier perspective(Campbell and Stanley 1963). Historical ballast for this view may be garnered fromthe field of experimental research in psychology, commonly dated to the publication ofGustav Theodor Fechner’s Elemente der Psychophysik in 1860. In this work, Hersen and



In order to see why this might be so, let us consider how a case studyof a single event – say, the French Revolution – works. Intuitively, sucha study provides an N of 1 (France). If one were to broaden the analysisto include a second revolution (e.g., the American Revolution), it wouldbe common to describe the study as comprising two observations. Yetthis is a gross distortion of what is really going on. The event known asthe French Revolution provides at least two observations, for it will beobserved over time to see what changed and what remained the same.These patterns of covariation offer essential empirical clues. They alsoconstruct multiple observations from an individual case. So N=2, at thevery least (e.g., before and after a revolution), in a case study of type 2(in Table 2.4).

If, instead, there is no temporal variation – if, for example, the FrenchRevolution is examined at a single point in time – then the investigation islikely to focus on cross-sectional covariational patterns within that case,a case study of type 3 (in Table 2.4). If the primary unit of analysis is thenation-state, then within-case cases might be constructed from provinces,localities, groups, or individuals. The possibilities for within-case analysisare, in principle, infinite. In their pathbreaking study of the InternationalTypographers Union, Lipset, Trow, and Coleman note the variety ofwithin-case evidence, which included union locals, union shops (withineach local), and individual members of the union.22 It is not hard tosee why within-case N often swamps cross-case N. This is bound to betrue wherever individuals comprise within-case observations. A singlenational survey will produce a much larger sample than any conceivablecross-country analysis. Thus, in many circumstances case studies oftype 3 comprise a larger N than cross-sectional analyses or time-series

Barlow (1976: 2–3) report, Fechner developed “measures of sensation through severalpsychophysical methods. With these methods, Fechner was able to determine sensorythresholds, just noticeable differences (JNDs) in various sense modalities. What is com-mon to these methods is the repeated measurement of a response at different intensities ordifferent locations of a given stimulus in an individual subject . . . It is interesting to notethat Fechner was one of the first to apply statistical methods to psychological problems.Fechner noticed that judgments of [JNDs] in the sensory modalities varied somewhatfrom trial to trial. To quantify this variation, or ‘error’ in judgment, he borrowed thenormal law of error, demonstrated that these ‘errors’ were normally distributed arounda mean, which then became the ‘true’ sensory threshold. This use of descriptive statis-tics anticipated the application of these procedures to groups of individuals at the turnof the century when traits of capabilities were also found to be normally distributedaround a mean.” Hersen and Barlow note that Fechner, the pioneer, “was concernedwith variability within the subject.” See also Queen (1928).

22 Lipset, Trow, and Coleman (1956: 422).



cross-sectional analyses. For example, a recent review of natural resourcemanagement studies found that the N of a study varies inversely with itsgeographic scope. Specifically, case studies focused on single communitiestend to have large samples, since they often employ individual-levelobservations; cross-case studies are more likely to treat communities ascomprising observations, and hence have a smaller N.23 This is a commonpattern.

Evidently, if a case study combines temporal and within-case variation,as in case studies of type 4, then its potential N increases accordingly. Andif cross-case analysis is added to this, as in the comparative method orthe comparative-historical method (types 5 and 6 in Table 2.4), then onerealizes a further enlargement in potential observations.

These facts hold true regardless of whether the method is experimen-tal or nonexperimental. It is also true of counterfactual reasoning, whichtypically consists of four observations – the actual (as it happened) beforeand after observations, and the before and after observations as recon-structed through counterfactual reasoning (i.e., with an imagined inter-vention). In short, the case study does not preclude a large N. It simplyprecludes a large cross-case N, by definition. Indeed, many renowned casestudies are data-rich and include extensive, and occasionally quite sophis-ticated, quantitative analysis. Frederic Le Play’s work on working-classfamilies incorporated hundreds of case studies.24 Robert and Helen Lynd’sstudy of Muncie, Indiana, featured surveys of hundreds of respondentsin “Middletown.”25 Yankee City, another pioneering community study,included interviews with 17,000 people.26

What, then, of the infamous N=1 research design that haunts theimaginations of social scientists everywhere?27 This hypothetical researchdesign occupies the empty cell in Table 2.4. The cell is empty because itrepresents a research design that is not logically feasible. A single caseobserved at a single point in time without the addition of within-caseobservations offers no evidence whatsoever of a causal proposition. Intrying to intuit a causal relationship from this snapshot one would beengaging in a truly random operation, since an infinite number of linesmight be drawn through that one data point. I do not think there are any

23 Poteete and Ostrom (2005: 11).24 Brooke (1970).25 Lynd and Lynd (1929/1956).26 Warner and Lunt (1941).27 Achen and Snidal (1989); Geddes (1990); Goldthorpe (1997); King, Keohane, and Verba

(1994); Lieberson (1985: 107–15; 1992, 1994).



examples of this sort of investigation in social science research. Thus, Iregard it as a myth rather than a method.28

The point becomes even clearer if we consider the case study in rela-tion to a time-series cross-section (TSCS) research design, as illustrated inTable 2.3. Let us imagine that cases are comprised of countries and thattemporal units are years; hence, the unit of analysis is the country-year. InTable 2.3, each case has five observations and thus represents a singlecountry observed over five years (T1–5). Now, consider the possibilityof constructing a case study from just one of these observations – a singlecountry at a single point in time. This seems an unlikely prospect, unless ofcourse there is significant within-case variation during that year. Perhapsthis country, during those twelve months, offers a critical juncture in whichthe variables of theoretical interest undergo a significant change. Whetherthe temporal era is short or long (and we can imagine much shorter andmuch longer temporal periods), the significant feature of most case stud-ies is that they look at periods of change, and these periods of changeproduce (or are regarded as producing) distinct observations – classically“before” (pre-) and “after” (post-) observations. Alternatively, it may bepossible to exploit spatial (cross-sectional) evidence in that country atthat particular time – for example, with extensive documentary recordsor a systematic survey. In these circumstances, one can easily imaginea case study being constructed from a single observation in a time-seriescross-section research design. But this can be accomplished only by subdi-viding the original observation into multiple observations. N is no longerequal to 1.

The skeptical reader may regard this conclusion as a semantic quibble,of little import to the real world of research. If so, she might considerthe following quite common research scenario. An ethnographic studyprovides a thick description, in prose, of a particular setting which isintended to uncover certain features of other settings (not studied). Theprose stretches for five hundred pages in a draft manuscript and is rather

28 The one possible exception is the deviant case that disproves a deterministic proposition.However, the utility of the deviant case rests upon a broader population of cases thatlies in the background of a case study focused on a single case. Thus, the N of such astudy, I would argue, is greater than one – even if no within-case evidence is gathered.The more important point is perhaps the following. No one has ever conducted a casestudy analysis that consists of only a single observation. If the point of the case study isto demonstrate that a single case of such-and-such a type exists (perhaps with the goalof falsifying a deterministic proposition), then it is likely to take a good deal of work toestablish the facts of that case. This work consists of multiple within-case observations.Again, the N is much higher than one.



repetitive; certain patterns are repeated again and again. In an effort toreduce the sheer volume of descriptive material, as well as to attain a moresynthetic analysis, the researcher begins to code the results of her laborsinto standardized categories: she counts. Has she, by committing the actof numeracy, now converted a case study into some other type of study?(If so, what shall we call it?) Note that the object of her study does notvary, even though the prose is now combined with some form of quanti-tative analysis, which may be simple or sophisticated. The introductionof statistical analysis does not – should not – disqualify a study as a “casestudy.”

The Style of Analysis

To be sure, non–case study work is by definition quantitative (“statisti-cal”) in nature. This is so because whenever one is attempting to incorpo-rate a large number of cases into a single analysis, it will be necessary toreduce the evidence to a small number of dimensions. One cannot explore1,000 cases on their own terms (i.e., in detail). (One might simply accu-mulate case study after case study in a compendious multivolume work.However, in order to reach any meaningful conclusions about this pile ofdata it will be necessary to reduce the informational overload, which iswhy God gave us statistics.)

With case study evidence, the situation is evidently more complicated.Case studies may employ a great variety of techniques – both quantitativeand qualitative – for the gathering and analysis of evidence. This is one ofthe intriguing qualities of case-study research and lends that research itscharacteristic flexibility. Thus, it seems fair to say that there is an electiveaffinity between the case study format and qualitative, small-N work,even though the latter is not definitionally entailed. Let us explore whythis might be so.

Case study research, by definition, is focused on a single, relativelybounded unit. That single unit may, or may not, afford opportunitiesfor large-N within-case analysis. Within-case evidence is sometimes quiteextensive, as when individual-level variation bears upon a group-levelinference. But not always.

Consider the following classic studies, each of which focuses on theattitudes and characteristics of American citizens. The American Voter, acollaborative effort by Angus Campbell, Philip Converse, Warren Miller,and Donald Stokes, examines public opinion on a wide range of topicsthat are thought to influence electoral behavior through the instrument



of a nationwide survey of the general public.29 The People’s Choice, byPaul Lazarsfeld, Bernard Berelson, and Hazel Gaudet, is a longitudinalpanel study focusing on 600 citizens living in Erie County, Ohio, whowere polled at monthly intervals during the 1940 presidential campaignto determine what influences the campaign may have had on their choiceof candidates.30 Middletown, by Robert and Helen Lynd, examines lifein a midsized city, including such topics as earning a living, making ahome, training the young, using leisure, taking part in religious prac-tices, and taking part in community activities (these are the sections intowhich the book is divided). The Lynds and their accomplices rely on agreat variety of evidence, including in-depth interviews, surveys, directobservation, secondary accounts, registers of books checked out of thelibrary, and so forth.31 Political Ideology, by Robert Lane, attempts touncover the sources of political values in a subsection of the Americanpublic, represented by fifteen subjects who are interviewed intensively bythe author. These subjects are male, white, married, fathers, between theages of twenty-five and fifty-four, working-class and white-collar, native-born, of varying religions, and living in an (unnamed) city on the easternseaboard.32

A summary of some of the methodological features of these four stud-ies is contained in Table 2.5. Note that the first two studies (The AmericanVoter and The People’s Choice) are classified as cross-case and the secondpair (Middletown and Political Ideology) as case studies. What is it thatdrives this distinction? Clearly, it is not the type of subjects under study(all focus primarily on individuals), the number of observations (whichrange from small-N to large-N), or the breadth of the population (all pur-port to describe features of the same country). The style of analysis differsin one respect: only in the case studies does qualitative analysis comprise asignificant portion of the research. This, in turn, is a product of the num-ber of cases under investigation. Where hundreds of individuals are beingstudied at once, there is no opportunity to evaluate cases in a qualitative

29 Campbell et al. (1960).30 Lazarsfeld, Berelson, and Gaudet (1948). A larger poll, with 2,000 respondents, was

taken initially, as a way of establishing a baseline for the chosen panel of 600. In addition,special attention was paid to those whose vote choice changed during the course of thepanel. These might be looked upon as a series of case studies nested within the largerpanel study. However, because this sort of analysis plays only a secondary role in theoverall analysis, it seems fair to characterize this research design as “cross-case.”

31 Lynd and Lynd (1929/1956).32 Lane (1962).



table 2.5. Case study and cross-case study research designs compared

Study Subjects Cases Largest Sample Analysis Population

The American Voter (Campbell et al.,

1960)

Citizens of the United

States

1,000+ (individuals) 1,000 + Quant Americans

Cross-casestudy

The People’s Choice (Lazarsfeld 1948)

Citizens of Erie County,

OH

600 (individuals)

2,000 Quant Americans

Middletown(Lynd and Lynd.

1929/1956)

Citizens of Muncie, IN

1 (cities)

300+Quant & Qual

Americancities

Casestudy

Political Ideology (Lane 1962)

Working men of “Eastport”

15 (individuals)

15 QualAmericanworking

class

All categories (subjects, cases, analysis, population) refer to the primary inferences produced bythe study in question.

manner. By contrast, where a single case (as in Middletown) or a smallnumber of cases (as in Political Ideology) is under study, qualitative anal-ysis is usually de rigueur – though it may be combined with quantitativeanalysis (as in Middletown).

The reader will notice that subtle differences in the research objectiveof a study can shift it from one category to another. If, for example,Robert and Helen Lynd decided to treat their surveys as representative ofindividuals in the general public (across the United States), rather than asrepresentative of cities in the United States, then Middletown would takeon the methodological features of The People’s Choice: it would becomea cross-case study. Indeed, this is a plausible reading of some portions ofthat study.

Importantly, the technique of analysis employed in a case study isnot simply a function of the sheer number of within-case observationsavailable in that unit. It is, more precisely, a function of the numberof comparable observations available within that unit. Consider RobertLane’s intensive interviews. Clearly, lots of “data” was recovered fromthese lengthy discussions. However, the respondents’ answers were notcoded so as to conform to standardized variables. Hence, they cannotbe handled within a dataset format, usually referred to as a “sample”(although we have occasionally employed this term in a broader sense).Of course, Lane could have chosen to recode these interviews to allow



for a quantitative analysis, reducing the diversity of the original informa-tion in order to conform to uniform parameters. It is not clear that muchwould have been gained by doing so. In the event, his study is limited toqualitative forms of analysis.

This issue is treated at length in a later chapter. For the moment, notethe fact that case study research often provides a piece of evidence pertain-ing to A, another piece of evidence pertaining to B, and a third pertainingto C. There may be many observations (in total), and they may all berelevant to a central causal argument, even though they are not directlycomparable to one another. These are referred to in Chapter Seven asnoncomparable observations.

In summary, large-N cross-case research is quantitative, by definition.This much conforms to usual perceptions. However, case study researchmay be either qualitative or quantitative, or both, depending upon thesort of within-case evidence that is available and relevant to the questionat hand. Consequently, the traditional association of case study work withqualitative methods is correctly regarded as a methodological affinity, nota definitional entailment. It is true sometimes, but not all the time.


3

What Is a Case Study Good For?

Case Study versus Large-N Cross-Case Analysis

In Chapter Two, I argued that the case study approach to research is mostusefully defined as an intensive study of a single unit or a small number ofunits (the cases), for the purpose of understanding a larger class of similarunits (a population of cases). This was put forth as a minimal defini-tion of the topic.1 In this chapter, I proceed to discuss the nondefinitionalattributes of the case study – attributes that are often, but not invari-ably, associated with the case study method. These will be understoodas methodological affinities flowing from our minimal definition of theconcept.2

The case study research design exhibits characteristic strengths andweaknesses relative to its large-N cross-case cousin. These trade-offsderive, first of all, from basic research goals such as (1) whether the study isoriented toward hypothesis generating or hypothesis testing, (2) whetherinternal or external validity is prioritized, (3) whether insight into causalmechanisms or causal effects is more valuable, and (4) whether the scopeof the causal inference is deep or broad. These trade-offs also hinge onthe shape of the empirical universe, that is, on (5) whether the popula-tion of cases under study is heterogeneous or homogeneous, (6) whether

1 My intention was to include only those attributes commonly associated with the case studymethod that are always implied by our use of the term, excluding those attributes that aresometimes violated by standard usage. For further discussion of minimal definitions, seeGerring (2001: Chapter 4); Gerring and Barresi (2003); and Sartori (1976).

2 These additional attributes might also be understood as comprising an ideal-type(“maximal”) definition of the topic (Gerring 2001: Chapter 4; Gerring and Barresi 2003).Recent evaluations of the strengths and weaknesses of case study research can be foundin Flyvbjerg (2004); Levy (2002a); and Verschuren (2001).

37



table 3.1. Case study and cross-case research designs: considerations

Affinity

Case Study Cross-Case Study

Research goals1. Hypothesis Generating Testing2. Validity Internal External3. Causal insight Mechanisms Effects4. Scope of proposition Deep Broad

Empirical factors5. Population of cases Heterogeneous Homogeneous6. Causal strength Strong Weak7. Useful variation Rare Common8. Data availability Concentrated Dispersed

Additional factors9. Causal complexity Indeterminate

10. State of the field Indeterminate

the causal relationship of interest is strong or weak, (7) whether usefulvariation on key parameters within that population is rare or common,and (8) whether available data is concentrated or dispersed. Along eachof these dimensions, case study research has an affinity for the first factor,and cross-case research has an affinity for the second, as summarized inTable 3.1.

I argue that other issues impinging upon the research format, suchas (9) causal complexity and (10) the state of research in a given field,are indeterminate in their implications. Sometimes these factors militatetoward a case study research design; at other times, toward a cross-caseresearch design.

To reiterate, the eight trade-offs depicted in Table 3.1 represent method-ological affinities, not invariant laws. Exceptions can be found to each one.Even so, these general tendencies are often noted in case study researchand have been reproduced in multiple disciplines and subdisciplines overthe course of many decades.

It should be stressed that each of these trade-offs carries a ceterisparibus caveat. Case studies are more useful for generating new hypothe-ses, all other things being equal. The reader must bear in mind thatnine additional factors also rightly influence a writer’s choice of researchdesign, and they may lean in the other direction. Ceteris is not alwaysparibus. One should not jump to conclusions about the research design


What Is a Case Study Good For? 39

appropriate to a given setting without considering the entire range ofissues involved – some of which may be more important than others.

Hypothesis: Generating versus Testing

Social science research involves a quest for new theories as well as a test-ing of existing theories; it is comprised of both “conjectures” and “refu-tations.”3 Regrettably, social science methodology has focused almostexclusively on the latter. The conjectural element of social science is usu-ally dismissed as a matter of guesswork, inspiration, or luck – a leap offaith, and hence a poor subject for methodological reflection.4 Yet it willreadily be granted that many works of social science, including most ofthe acknowledged classics, are seminal rather than definitive. Their classicstatus derives from the introduction of a new idea or a new perspectivethat is subsequently subjected to more rigorous (and refutable) analysis.Indeed, it is difficult to devise a program of falsification the first time a newtheory is proposed. Path-breaking research, almost by definition, is pro-tean. Subsequent research on that topic tends to be more definitive insofaras its primary task is limited to verify or falsify a preexisting hypothesis.Thus, the world of social science may be usefully divided according to thepredominant goal undertaken in a given study, either hypothesis generat-ing or hypothesis testing. There are two moments of empirical research,a “lightbulb” moment and a skeptical moment, each of which is essentialto the progress of a discipline.5

Case studies enjoy a natural advantage in research of an exploratorynature. Several millennia ago, Hippocrates reported what were, arguably,the first case studies ever conducted. They were fourteen in number.6

Darwin’s insights into the process of human evolution came after his

3 Popper (1963).4 Karl Popper (quoted in King, Keohane, and Verba 1994: 14) writes: “there is no such thing

as a logical method of having new ideas. . . . Discovery contains ‘an irrational element,’ ora ‘creative intuition.’” One recent collection of essays and interviews takes new ideas asits special focus (Munck and Snyder 2006), though it may be doubted whether there aregeneralizable results.

5 Gerring (2001: Chapter 10). The trade-off between these two styles of research is implicitin Achen and Snidal (1989); the authors criticize the case study for its deficits in the lattergenre but also acknowledge the benefits of the case study along the former dimension (ibid.,167–8). Reichenbach also distinguishes between a “context of discovery” and a “contextof justification.” Likewise, Peirce’s concept of abduction recognizes the importance of agenerative component in science.

6 Bonoma (1985: 199). Some of the following examples are discussed in Patton (2002:245).



travels to a few select locations, notably Easter Island. Freud’s revolu-tionary work on human psychology was constructed from a close obser-vation of fewer than a dozen clinical cases. Piaget formulated his theoryof human cognitive development while watching his own two childrenas they passed from childhood to adulthood. Levi-Strauss’s structuralisttheory of human cultures built on the analysis of several North and SouthAmerican tribes. Douglass North’s neoinstitutionalist theory of economicdevelopment was constructed largely through a close analysis of a hand-ful of early developing states (primarily England, the Netherlands, andthe United States).7 Many other examples might be cited of seminal ideasthat derived from the intensive study of a few key cases.

Evidently, the sheer number of examples of a given phenomenon doesnot, by itself, produce insight. It may only confuse. How many times didNewton observe apples fall before he recognized the nature of gravity?This is an apocryphal example, but it illustrates a central point: casestudies may be more useful than cross-case studies when a subject is beingencountered for the first time or is being considered in a fundamentallynew way. After reviewing the case study approach to medical research,one researcher finds that although case reports are commonly regarded asthe lowest or weakest form of evidence, they are nonetheless understoodto comprise “the first line of evidence.” The hallmark of case reporting,according to Jan Vandenbroucke, “is to recognize the unexpected.” Thisis where discovery begins.8

The advantages that case studies offer in work of an exploratory naturemay also serve as impediments in work of a confirmatory/disconfirmatorynature. Let us briefly explore why this might be so.9

Traditionally, scientific methodology has been defined by a segregationof conjecture and refutation. One should not be allowed to contaminatethe other.10 Yet in the real world of social science, inspiration is oftenassociated with perspiration. “Lightbulb” moments arise from a closeengagement with the particular facts of a particular case. Inspiration ismore likely to occur in the laboratory than in the shower.

The circular quality of conjecture and refutation is particularly appar-ent in case study research. Charles Ragin notes that case study research

7 North and Weingast (1989); North and Thomas (1973).8 Vandenbroucke (2001: 331).9 For discussion of this trade-off in the context of economic growth theory, see Temple

(1999: 120).10 Geddes (2003); King, Keohane, and Verba (1994); Popper (1934/1968).



is all about “casing” – defining the topic, including the hypothesis(es) ofprimary interest, the outcome, and the set of cases that offer relevant infor-mation vis-a-vis the hypothesis.11 A study of the French Revolution maybe conceptualized as a study of revolution, of social revolution, of revolt,of political violence, and so forth. Each of these topics entails a differentpopulation and a different set of causal factors. A good deal of authorialintervention is necessary in the course of defining a case study topic, forthere is a great deal of evidentiary leeway. Yet the subjectivity of casestudy research allows for the generation of a great number of hypotheses,insights that might not be apparent to the cross-case researcher who workswith a thinner set of empirical data across a large number of cases and witha more determinate (fixed) definition of cases, variables, and outcomes.It is the very fuzziness of case studies that grants them an advantage inresearch at the exploratory stage, for the single-case study allows one totest a multitude of hypotheses in a rough-and-ready way. Nor is this anentirely conjectural process. The relationships discovered among differentelements of a single case have a prima facie causal connection: they are allat the scene of the crime. This is revelatory when one is at an early stageof analysis, for at that point there is no identifiable suspect and the crimeitself may be difficult to discern. The fact that A, B, and C are presentat the expected times and places (relative to some outcome of interest) issufficient to establish them as independent variables. Proximal evidenceis all that is required. Hence, the common identification of case studies as“plausibility probes,” “pilot studies,” “heuristic studies,” “exploratory”and “theory-building” exercises.12

A large-N cross-case study, by contrast, generally allows for the testingof only a few hypotheses but does so with a somewhat greater degree ofconfidence, as is appropriate to work whose primary purpose is to testan extant theory. There is less room for authorial intervention becauseevidence gathered from a cross-case research design can be interpretedin a limited number of ways. It is therefore more reliable. Another wayof stating the point is to say that while case studies lean toward Type1 errors (falsely rejecting the null hypothesis), cross-case studies leantoward Type 2 errors (failing to reject the false null hypothesis). Thisexplains why case studies are more likely to be paradigm-generating, whilecross-case studies toil in the prosaic but highly structured field of normalscience.

11 Ragin (1992b).12 Eckstein (1975); Ragin (1992a, 1997); Rueschemeyer and Stephens (1997).



I do not mean to suggest that case studies never serve to confirm ordisconfirm hypotheses. Evidence drawn from a single case may falsify anecessary or sufficient hypothesis, as will be discussed. Additionally, casestudies are often useful for the purpose of elucidating causal mechanisms,and this obviously affects the plausibility of an X/Y relationship. However,general theories rarely offer the kind of detailed and determinate predic-tions on within-case variation that would allow one to reject a hypothesisthrough pattern matching (without additional cross-case evidence). The-ory testing is not the case study’s strong suit. The selection of “crucial”cases is at pains to overcome the fact that the cross-case N is minimal (seeChapter Five). Thus, one is unlikely to reject a hypothesis, or to considerit definitively proved, on the basis of a single case.

Harry Eckstein himself acknowledged that his argument for case stud-ies as a form of theory confirmation was largely hypothetical. At the timeof writing, several decades ago, he could not point to any social sciencestudy where a crucial case study had performed the heroic role assignedto it.13 I suspect that this is still more or less true. Indeed, it is true even ofexperimental case studies in the natural sciences. “We must recognize,”note Donald Campbell and Julian Stanley,

that continuous, multiple experimentation is more typical of science than once-and-for-all definitive experiments. The experiments we do today, if successful,will need replication and cross-validation at other times under other conditionsbefore they can become an established part of science. . . . [E]ven though we rec-ognize experimentation as the basic language of proof . . . we should not expectthat ‘crucial experiments’ which pit opposing theories will be likely to have clear-cut outcomes. When one finds, for example, that competent observers advocatestrongly divergent points of view, it seems likely on a priori grounds that bothhave observed something valid about the natural situation, and that both rep-resent a part of the truth. The stronger the controversy, the more likely this is.Thus we might expect in such cases an experimental outcome with mixed results,or with the balance of truth varying subtly from experiment to experiment. Themore mature focus . . . avoids crucial experiments and instead studies dimensionalrelationships and interactions along many degrees of the experimental variables.14

A single case study is still a single-shot affair – a single example of a largerphenomenon.

The trade-off between hypothesis generating and hypothesis testinghelps us to reconcile the enthusiasm of case study researchers and theskepticism of case study critics. They are both right, for the looseness of

13 Eckstein (1975).14 Campbell and Stanley (1963: 3).



case study research is a boon to new conceptualizations just as it is a baneto falsification.

Validity: Internal versus External

Questions of validity are often distinguished according to those that areinternal to the sample under study and those that are external (i.e., apply-ing to a broader – unstudied – population). The latter may be conceptual-ized as a problem of representativeness between sample and population.Cross-case research is always more representative of the population ofinterest than case study research, so long as some sensible procedure ofcase selection is followed (presumably some version of random sampling,as discussed in Chapter Five). Case study research suffers problems of rep-resentativeness because it includes, by definition, only a small number ofcases of some more general phenomenon. Are the men chosen by RobertLane typical of white, immigrant, working-class American males?15 IsMiddletown representative of other cities in America?16 These sorts ofquestions forever haunt case study research. This means that case studyresearch is generally weaker with respect to external validity than its cross-case cousin.

The corresponding virtue of case study research is its internal valid-ity. Often, though not invariably, it is easier to establish the veracity of acausal relationship pertaining to a single case (or a small number of cases)than for a larger set of cases. Case study researchers share the bias ofexperimentalists in this respect: they tend to be more disturbed by threatsto within-sample validity than by threats to out-of-sample validity. Thus,it seems appropriate to regard the trade-off between external and inter-nal validity, like other trade-offs, as intrinsic to the cross-case/single-casechoice of research design.

Causal Insight: Causal Mechanisms versus Causal Effects

A third trade-off concerns the sort of insight into causation that aresearcher intends to achieve. Two goals may be usefully distinguished.The first concerns an estimate of the causal effect; the second concernsthe investigation of a causal mechanism (i.e., a pathway from X to Y).

15 Lane (1962).16 Lynd and Lynd (1929/1956).



When I say “causal effect,” I refer to two things: (a) the magnitude of acausal relationship (the expected effect on Y of a given change in X acrossa population of cases) and (b) the relative precision or uncertainty of thatpoint estimate.17 Evidently, it is difficult to arrive at a reliable estimateof causal effects across a population of cases by looking at only a singlecase or a small number of cases. (The one possible exception would be anexperiment in which a given case can be tested repeatedly, returning toa virgin condition after each test. But here one faces inevitable questionsabout the representativeness of that much-studied case.)18 Thus, the esti-mate of a causal effect is almost always grounded in cross-case evidence.

It is now well established that causal arguments depend not only onmeasuring causal effects, but also on the identification of a causal mech-anism.19 That is, X must be connected with Y in a plausible fashion;otherwise, it is unclear whether a pattern of covariation is truly causal innature, or what the causal interaction might be. Moreover, without a clearunderstanding of the causal pathway(s) at work in a causal relationship,it is impossible to specify the model accurately, to identify possible instru-ments for the regressor of interest (if there are problems of endogeneity),or to interpret the results.20 Thus, causal mechanisms are presumed inevery estimate of a mean (average) causal effect.

In the task of investigating causal mechanisms, cross-case studies areoften not so illuminating. It has become a common criticism of large-Ncross-national research – for example, into the causes of growth, democ-racy, civil war, and other national-level outcomes – that such studiesdemonstrate correlations between inputs and outputs without clarifyingthe reasons for those correlations (i.e., clear causal pathways). We learn,

17 The correct estimation of a causal effect rests upon the optimal choice among possibleestimators. It therefore follows from the previous discussion that sample-based analysesare also essential for choosing among different estimators – as judged by their relativeefficiency and bias, among other desiderata. See Kennedy (2003) for a discussion of theseissues.

18 Note that the intensive study of a single unit may be a perfectly appropriate way toestimate causal effects within that unit. Thus, if one is interested in the relationshipbetween welfare benefits and work effort in the United States, one might obtain a moreaccurate assessment by examining data drawn from the United States alone, rather thancross-nationally. However, since the resulting generalization does not extend beyond theunit in question, this is not a case study in the usual sense.

19 Achen (2002); Dessler (1991); Elster (1998); George and Bennett (2005); Gerring (2005);Hedstrom and Swedberg (1998); Mahoney (2001); Tilly (2001).

20 In a discussion of instrumental variables in two-stage least squares analysis, Angrist andKrueger (2001: 8) note that “good instruments often come from detailed knowledge ofthe economic mechanism, institutions determining the regressor of interest.”



for example, that infant mortality is strongly correlated with state fail-ure;21 but it is quite another matter to interpret this finding, which is con-sistent with a number of different causal mechanisms. Sudden increases ininfant mortality might be the product of famine, of social unrest, of newdisease vectors, of government repression, and of countless other factors,some of which might be expected to impact the stability of states, andothers of which are more likely to be a result of state instability.

Case studies, if well constructed, may allow one to peer into the box ofcausality to locate the intermediate factors lying between some structuralcause and its purported effect. Ideally, they allow one to “see” X andY interact – Hume’s billiard ball crossing the table and hitting a secondball.22 Barney Glaser and Anselm Strauss point out that in field work“general relations are often discovered in vivo; that is, the field workerliterally sees them occur.”23 When studying decisional behavior, case studyresearch may offer insight into the intentions, the reasoning capabilities,and the information-processing procedures of the actors involved in agiven setting. Thus, Dennis Chong uses in-depth interviews with a verysmall sample of respondents in order to better understand the process bywhich people reach decisions about civil liberties issues. Chong comments:

One of the advantages of the in-depth interview over the mass survey is that itrecords more fully how subjects arrive at their opinions. While we cannot actuallyobserve the underlying mental process that gives rise to their responses, we canwitness many of its outward manifestations. The way subjects ramble, hesitate,stumble, and meander as they formulate their answers tips us off to how they arethinking and reasoning through political issues.24

Similarly, the investigation of a single case may allow one to test thecausal implications of a theory, thus providing corroborating evidencefor a causal argument. This is sometimes referred to as pattern matching(see Chapter Seven).

One example of case study evidence calling into question a generaltheoretical argument on the basis of an investigation of causal mecha-nisms concerns the theory of rational deterrence. Deterrence theory, as

21 Goldstone et al. (2000).22 This has something to do with the existence of process-tracing evidence, a matter to

be discussed later. But it is not necessarily predicated on this sort of evidence. Sensitivetime-series data, another specialty of the case study, is also relevant to the question ofcausal mechanisms.

23 Glaser and Strauss (1967: 40).24 Chong (1993: 868). For other examples of in-depth interviewing, see Hochschild (1981)

and Lane (1962).



it was understood in the 1980s, presupposes a number of key assump-tions, namely, that “actors have exogenously given preferences and choiceoptions, and [that] they seek to optimize preferences in light of otheractors’ preferences and options . . . , [that] variation in outcomes is tobe explained by differences in actors’ opportunities . . . , and [that] thestate acts as if it were a unitary rational actor.”25 A generation of casestudies, however, suggests that, somewhat contrary to theory, (a) interna-tional actors often employ “shortcuts” in their decision-making processes(i.e., they do not make decisions de novo, based purely on an analysis ofpreferences and possible consequences); (b) a strong cognitive bias existsbecause of “historical analogies to recent important cases that the personor his country has experienced firsthand” (e.g., “Somalia = Vietnam”);(c) “accidents and confusion” are often manifest in international crises;(d) a single important value or goal often trumps other values (in a hastyand ill-considered manner); and (e) actors’ impressions of other actorsare strongly influenced by their self-perceptions (information is highlyimperfect). In addition to these cognitive biases, there is a series of psy-chological biases.26 In sum, while the theory of deterrence may still hold,the causal pathways contained in this theory seem to be considerably morevariegated than previous work based on cross-case research had led us tobelieve. In-depth studies of particular international incidents have beenhelpful in uncovering these complexities.27

Dietrich Rueschemeyer and John Stephens offer a second example ofhow an examination of causal mechanisms may call into question a gen-eral theory based on cross-case evidence. The thesis of interest concernsthe role of British colonialism in fostering democracy among post-colonialregimes. In particular, the authors investigate the diffusion hypothesis,that democracy was enhanced by “the transfer of British governmentaland representative institutions and the tutoring of the colonial people inthe ways of British government.” On the basis of in-depth analysis ofseveral cases, the authors report:

We did find evidence of this diffusion effect in the British settler colonies of NorthAmerica and the Antipodes; but in the West Indies, the historical record pointsto a different connection between British rule and democracy. There the Britishcolonial administration opposed suffrage extension, and only the white elites were

25 Achen and Snidal (1989: 150).26 Jervis (1989: 196). See also George and Smoke (1974).27 George and Smoke (1974: 504). For another example of case study work that tests

theories based upon predictions about causal mechanisms, see McKeown (1983).



‘tutored’ in the representative institutions. But, critically, we argued on the basis ofthe contrast with Central America, British colonialism did prevent the local plan-tation elites from controlling the local state and responding to the labor rebellionof the 1930s with massive repression. Against the adamant opposition of thatelite, the British colonial rulers responded with concessions which allowed for thegrowth of the party-union complexes rooted in the black middle and workingclasses, which formed the backbone of the later movement for democracy andindependence. Thus, the narrative histories of these cases indicate that the robuststatistical relation between British colonialism and democracy is produced only inpart by diffusion. The interaction of class forces, state power, and colonial policymust be brought in to fully account for the statistical result.28

Whether or not Rueschemeyer and Stephens are correct in their conclu-sions need not concern us here. What is critical, however, is that anyattempt to deal with this question of causal mechanisms is heavily relianton evidence drawn from case studies. In this instance, as in many oth-ers, the question of causal pathways is simply too difficult, requiring toomany poorly measured or unmeasurable variables, to allow for accuratecross-sectional analysis.29

To be sure, causal mechanisms do not always require explicit atten-tion. They may be quite obvious. And in other circumstances, they maybe amenable to cross-case investigation. For example, a sizeable litera-ture addresses the causal relationship between trade openness and thewelfare state. The usual empirical finding is that more open economiesare associated with greater social welfare spending. The question then

28 Rueschemeyer and Stephens (1997: 62).29 A third example of case study analysis focused on causal mechanisms concerns policy

delegation within coalition governments. Michael Thies (2001) tests two theories abouthow parties delegate power. The first, known as ministerial government, supposes thatparties delegate ministerial portfolios in toto to one of their members (the party whoseminister holds the portfolio). The second theory, dubbed managed delegation, supposesthat members of a multiparty coalition delegate power, but also actively monitor theactivity of ministerial posts held by other parties. The critical piece of evidence used totest these rival theories is the appointment of junior ministers (JMs). If JMs are from thesame party as the minister, we can assume that the ministerial government model is inoperation. If the JMs are from different parties, Thies infers that a managed delegationmodel is in operation, where the JM is assumed to perform an oversight function regard-ing the activity of the bureau in question. This empirical question is explored acrossfour countries – Germany, Italy, Japan, and the Netherlands – providing a series of casestudies focused on the internal workings of parliamentary government. (I have simplifiedthe nature of the evidence in this example, which extends not only to the simple pres-ence or absence of cross-partisan JMs but also to a variety of additional process-tracingclues.) Other good examples of within-case research that shed light on a broader theorycan be found in Canon (1999); Martin (1992); Martin and Swank (2004); and Young(1999).



becomes why such a robust correlation exists. What are the plausibleinterconnections between trade openness and social welfare spending?One possible causal path, suggested by David Cameron,30 is that increasedtrade openness leads to greater domestic economic vulnerability to exter-nal shocks (due, for instance, to changing terms of trade). If that is true,one should find a robust correlation between annual variations in a coun-try’s terms of trade (a measure of economic vulnerability) and social wel-fare spending. As it happens, the correlation is not robust, and this leadssome commentators to doubt whether the putative causal mechanism pro-posed by David Cameron and many others is actually at work.31 Thus, ininstances where an intervening variable can be effectively operationalizedacross a large sample of cases, it may be possible to test causal mechanismswithout resorting to case study investigation.32

Even so, the opportunities for investigating causal pathways are gener-ally more apparent in a case study format. Consider the contrast betweenformulating a standardized survey for a large group of respondents andformulating an in-depth interview with a single subject or a small set ofsubjects, such as that undertaken by Dennis Chong in the previous exam-ple. In the latter situation, the researcher is able to probe into details thatwould be impossible to delve into, let alone anticipate, in a standardizedsurvey. She may also be in a better position to make judgments as to theveracity and reliability of the respondent. Tracing causal mechanisms isabout cultivating sensitivity to a local context. Often, these local contextsare essential to cross-case testing. Yet the same factors that render casestudies useful for micro-level investigation also make them less useful formeasuring mean (average) causal effects. It is a classic trade-off.

Scope of Proposition: Deep versus Broad

The utility of a case study mode of analysis is in part a product of the scopeof the causal argument that a researcher wishes to prove or demonstrate.Arguments that strive for great breadth are usually in greater need of cross-case evidence; causal arguments restricted to a small set of cases can moreplausibly subsist on the basis of a single-case study. The extensive/intensivetrade-off is fairly commonsensical.33 A case study of France probably

30 Cameron (1978).31 Alesina, Glaeser, and Sacerdote (2001).32 For additional examples of this nature, see Feng (2003); Papyrakis and Gerlagh (2003);

and Ross (2001).33 Eckstein (1975: 122).



offers more useful evidence for an argument about Europe than for anargument about the whole world. Propositional breadth and evidentiarybreadth generally go hand in hand.

Granted, there are a variety of ways in which single-case studies cancredibly claim to provide evidence for causal propositions of broad reach –for example, by choosing cases that are especially representative of thephenomenon under study (“typical” cases) or by choosing cases that rep-resent the most difficult scenario for a given proposition and are thusbiased against the attainment of certain results (“crucial” cases), as dis-cussed in Chapter Five. Even so, a proposition with a narrow scope ismore conducive to case study analysis than a proposition with a broadpurview, all other things being equal. The breadth of an inference thusconstitutes one factor, among many, in determining the utility of the casestudy mode of analysis. This is reflected in the hesitancy of many casestudy researchers to invoke determinate causal propositions with greatreach – “covering laws,” in the idiom of philosophy of science.

By the same token, one of the primary virtues of the case study methodis the depth of analysis that it offers. One may think of depth as referringto the detail, richness, completeness, wholeness, or the degree of variancein an outcome that is accounted for by an explanation. The case studyresearcher’s complaint about the thinness of cross-case analysis is welltaken; such studies often have little to say about individual cases. Other-wise stated, cross-case studies are likely to explain only a small portion ofthe variance with respect to a given outcome. They approach that outcomeat a very general level. Typically, a cross-case study aims only to explainthe occurrence/nonoccurrence of a revolution, while a case study mightalso strive to explain specific features of that event – why it occurredwhen it did and in the way that it did. Case studies are thus rightlyidentified with “holistic” analysis and with the “thick” description ofevents.34

Whether to strive for breadth or depth is not a question that canbe answered in any definitive way. All we can safely conclude is thatresearchers invariably face a choice between knowing more about less, orless about more. The case study method may be defended, as well as criti-cized, along these lines.35 Indeed, arguments about the “contextual sensi-tivity” of case studies are perhaps more precisely (and fairly) understoodas arguments about depth and breadth. The case study researcher who

34 My use of the term “thick” is somewhat different from the usage in Geertz (1973).35 See Ragin (2000: 22).



feels that cross-case research on a topic is insensitive to context is usuallynot arguing that nothing at all is consistent across the chosen cases. Rather,the case study researcher’s complaint is that much more could be said –accurately – about the phenomenon in question with a reduction in infer-ential scope.36

Indeed, I believe that a number of traditional issues related to casestudy research can be understood as the product of this basic trade-off.For example, case study research is often lauded for its holistic approachto the study of social phenomena in which behavior is observed in nat-ural settings. Cross-case research, by contrast, is criticized for its con-struction of artificial research designs that decontextualize the realm ofsocial behavior by employing abstract variables that seem to bear slightrelationship to the phenomena of interest.37 These associated congratula-tions and critiques may be understood as a conscious choice on the partof case study researchers to privilege depth over breadth.

The Population of Cases: Heterogeneous versus Homogeneous

The choice between a case study and cross-case style of analysis is drivennot only by the goals of the researcher, as just reviewed, but also bythe shape of the empirical universe that the researcher is attempting tounderstand. Consider, for starters, that the logic of cross-case analysis ispremised on some degree of cross-unit comparability (unit homogeneity).Cases must be similar to each other in whatever respects might affectthe causal relationship that the writer is investigating, or such differencesmust be controlled for. Uncontrolled heterogeneity means that cases are“apples and oranges”; one cannot learn anything about underlying causalprocesses by comparing their histories. The underlying factors of interestmean different things in different contexts (conceptual stretching), or theX/Y relationship of interest is different in different contexts (unit hetero-geneity).

Case study researchers are often suspicious of large-sample research,which, they suspect, contains heterogeneous cases whose differences can-not easily be modeled. “Variable-oriented” research is said to involveunrealistic “homogenizing assumptions.”38 In the field of international

36 Ragin (1987: Chapter 2). Herbert Blumer’s (1969: Chapter 7) complaints, however, aremore far-reaching.

37 Orum, Feagin, and Sjoberg (1991: 7).38 Ragin (2000: 35). See also Abbott (1990); Bendix (1963); Meehl (1954); Przeworski and

Teune (1970: 8–9); Ragin (1987; 2004: 124); Znaniecki (1934: 250–1).



relations, for example, it is common to classify cases according to whetherthey are deterrence failures or deterrence successes. However, AlexanderGeorge and Richard Smoke point out that “the separation of the depen-dent variable into only two subclasses, deterrence success and deterrencefailure,” neglects the great variety of ways in which deterrence can fail.Deterrence, in their view, has many independent causal paths (causal equi-finality), and these paths may be obscured when a study lumps heteroge-neous cases into a common sample.39

Another example, drawn from clinical work in psychology, concernsheterogeneity among a sample of individuals. Michel Hersen and DavidBarlow explain:

Descriptions of results from 50 cases provide a more convincing demonstration ofthe effectiveness of a given technique than separate descriptions of 50 individualcases. The major difficulty with this approach, however, is that the category inwhich these clients are classified most always becomes unmanageably heteroge-neous. ‘Neurotics,’ [for example], . . . may have less in common than any groupof people one would choose randomly. When cases are described individually,however, a clinician stands a better chance of gleaning some important informa-tion, since specific problems and specific procedures are usually described in moredetail. When one lumps cases together in broadly defined categories, individualcase descriptions are lost and the ensuing report of percentage success becomesmeaningless.40

Under circumstances of extreme case-heterogeneity, the researcher maydecide that she is better off focusing on a single case or a small numberof relatively homogeneous cases. Within-case evidence, or cross-case evi-dence drawn from a handful of most-similar cases, may be more usefulthan cross-case evidence, even though the ultimate interest of the inves-tigator is in a broader population of cases. Suppose one has a popula-tion of very heterogeneous cases, one or two of which undergo quasi-experimental transformations. Probably, one gains greater insight intocausal patterns throughout the population by examining these cases indetail than by undertaking a large-N cross-case analysis. By the sametoken, if the cases available for study are relatively homogeneous, thenthe methodological argument for cross-case analysis is correspondinglystrong. The inclusion of additional cases is unlikely to compromise theresults of the investigation, because these additional cases are sufficientlysimilar to provide useful information.

39 George and Smoke (1974: 514).40 Hersen and Barlow (1976: 11).



The issue of population heterogeneity/homogeneity may be under-stood, therefore, as a trade-off between N (observations) and K (vari-ables). If, in the quest to explain a particular phenomenon, each potentialcase offers only one observation and also requires one control variable (toneutralize heterogeneities in the resulting sample), then one loses degreesof freedom with each additional case. There is no point in using cross-caseanalysis or in extending a two-case study to further cases. If, on the otherhand, each additional case is relatively cheap – if no control variables areneeded, or if the additional case offers more than one useful observation(through time) – then a cross-case research design may be warranted.41 Toput the matter more simply, when adjacent cases are unit-homogeneous,the addition of more cases is easy, for there is no (or very little) het-erogeneity to model. When adjacent cases are heterogeneous, additionalcases are expensive, for every added heterogeneous element must be cor-rectly modeled, and each modeling adjustment requires a separate (andprobably unverifiable) assumption. The more background assumptionsare required in order to make a causal inference, the more tenuous thatinference is. This is not simply a question of attaining statistical signifi-cance. The ceteris paribus assumption at the core of all causal analysis isbrought into question (see Chapter 6). In any case, the argument betweencase study and cross-case research designs is not about causal complexityper se (in the sense in which this concept is usually employed), but ratherabout the trade-off between N and K in a particular empirical realm,and about the ability to model case-heterogeneity through statisticallegerdemain.42

Before concluding this discussion, it is important to point out thatresearchers’ judgments about case comparability are not, strictly speak-ing, matters that can be empirically verified. To be sure, one can look –and ought to look – for empirical patterns among potential cases. If thosepatterns are strong, then the assumption of case comparability seemsreasonably secure; and if they are not, then there are grounds for doubt.However, debates about case comparability usually concern borderlineinstances. Consider that many phenomena of interest to social scientistsare not rigidly bounded. If one is studying democracies, there is always

41 Shalev (1998).42 To be sure, if adjacent cases are identical, the phenomenon of interest is invariant. In that

case the researcher gains nothing at all by studying more examples of a phenomenon,for the results obtained with the first case will simply be replicated. However, virtuallyall phenomena of interest to social scientists has some degree of heterogeneity (casesare not identical), some stochastic element. Thus, the theoretical possibility of identical,invariant cases is rarely met in practice.



a question of how to define a democracy, and therefore of determininghow high or low the threshold for inclusion in the sample should be.Researchers have different ideas about this, and these ideas can hardlybe tested in a rigorous fashion. Similarly, there are long-standing disputesabout whether it makes sense to lump poor and rich societies together in asingle sample, or whether these constitute distinct populations. Again, theborderline between poor and rich (or “developed” and “undeveloped”) isblurry, and the notion of hiving off one from the other for separate analy-sis questionable, and unresolvable on purely empirical grounds. There isno safe (or “conservative”) way to proceed. A final sticking point concernsthe cultural/historical component of social phenomena. Many case studyresearchers feel that to compare societies with vastly different cultures andhistorical trajectories is meaningless. Yet many cross-case researchers feelthat to restrict one’s analytic focus to a single cultural or geographic regionis highly arbitrary, and equally meaningless. In these situations, it is evi-dently the choice of the researcher how to understand case homogeneity/heterogeneity across the potential populations of an inference. Where dolike cases end and unlike cases begin?

Because this issue is not, strictly speaking, empirical, it may be referredto as an ontological element of research design. An ontology is a visionof the world as it really is, a more or less coherent set of assumptionsabout how the world works, a research Weltanschauung analogous to aKuhnian paradigm.43 While it seems odd to bring ontological issues intoa discussion of social science methodology, it may be granted that socialscience research is not a purely empirical endeavor. What one finds iscontingent upon what one looks for, and what one looks for is to someextent contingent upon what one expects to find. Stereotypically, casestudy researchers tend to have a “lumpy” vision of the world; they seecountries, communities, and persons as highly individualized phenomena.Cross-case researchers, by contrast, have a less differentiated vision ofthe world; they are more likely to believe that things are pretty much thesame everywhere, at least as respects basic causal processes. These basicassumptions, or ontologies, drive many of the choices made by researcherswhen scoping out appropriate ground for research.

Causal Strength: Strong versus Weak

Regardless of whether the population is homogeneous or heterogeneous,relationships are easier to study if the true causal effect is strong, rather

43 Gutting (1980); Hall (2003); Kuhn (1962/1970); Wolin (1968).



than weak. Causal “strength” refers here to the magnitude and consis-tency of X’s effect on Y across a population of cases. (It involves both theshape of the evidence at hand and whatever priors might be relevant toan interpretation of that evidence.) Where X1 has a strong effect on Y itwill be relatively easy to study this relationship. Weak relationships, bycontrast, are often difficult to discern. This much is commonsensical, andapplies to all research designs.

For our purposes, what is significant is that weak causal relationshipsare particularly opaque when encountered in a case study format. Thus,there is a methodological affinity between weak causal relationships andlarge-N cross-case analysis, and between strong causal relationships andcase study analysis.

This point is clearest at the extremes. The strongest species of causalrelationships may be referred to as deterministic, where X is assumed to benecessary and/or sufficient for Y’s occurrence. A necessary and sufficientcause accounts for all of the variation on Y. A sufficient cause accounts forall of the variation in certain instances of Y. A necessary cause accounts,by itself, for the absence of Y. In all three situations, the relationship isusually assumed to be perfectly consistent, that is, invariant. There are noexceptions.

It should be clear why case study research designs have an easier timeaddressing causes of this type. Consider that a deterministic causal propo-sition can be disproved with a single case.44 For example, the reigning the-ory of political stability once stipulated that only in countries that wererelatively homogeneous, or where existing heterogeneity was mitigatedby cross-cutting cleavages, would social peace endure.45 Arend Lijphart’scase study of the Netherlands, a country with reinforcing social cleav-ages and very little social conflict, disproved this deterministic theory onthe basis of a single case.46 (One may dispute whether the original the-ory is correctly understood as deterministic. However, if it is, then it hasbeen decisively refuted by a single case study.) Proving an invariant causalargument generally requires more cases. However, it is not nearly as com-plicated as proving a probabilistic argument, for the simple reason thatone assumes invariant relationships; consequently, the single case understudy carries more weight. Stochastic variation is ruled out.

44 Dion (1998).45 Almond (1956); Bentley (1908/1967); Lipset (1960/1963); Truman (1951).46 Lijphart (1968); see also Lijphart (1969). For additional examples of case studies discon-

firming general propositions of a deterministic nature, see Allen (1965); Lipset, Trow,and Coleman (1956); Njolstad (1990); and the discussion in Rogowski (1995).



Magnitude and consistency – the two components of causal strength –are usually matters of degree. It follows that the more tenuous the con-nection between X and Y, the more difficult it will be to address in acase study format. This is because the causal mechanisms connecting Xwith Y are less likely to be detectable in a single case when the totalimpact is slight or highly irregular. It is no surprise, therefore, that thecase study research design has, from the very beginning, been associatedwith causal arguments that are deterministic, while cross-case researchhas been associated with causal arguments that are assumed to be slightand highly probabilistic.47 (Strictly speaking, magnitude and consistencyare independent features of a causal relationship. However, because theytend to covary, and because we tend to conceptualize them in tandem, Itreat them as components of a single dimension.)

Now, let us consider an example drawn from the other extreme. Thereis generally assumed to be a weak relationship between regime typeand economic performance. Democracy, if it has any effect on economicgrowth at all, probably has only a slight effect over the near to mediumterm, and this effect is probably characterized by many exceptions (casesthat do not fit the general pattern). This is because many things otherthan democracy affect a country’s growth performance, and because theremay be a significant stochastic component in economic growth (factorsthat cannot be modeled in a general way). Because of the diffuse natureof this relationship it will probably be difficult to gain insight by look-ing at a single case. Weak relationships are difficult to observe in oneinstance. Note that even if there seems to be a strong relationship betweendemocracy and economic growth in a given country, it may be questionedwhether this case is typical of the larger population of interest, given thatwe have already stipulated that the typical magnitude of this relation-ship is diminutive and irregular. Of course, the weakness of democracy’spresumed relationship to growth is also a handicap in cross-case anal-ysis. A good deal of criticism has been directed toward studies of thistype, where findings are rarely robust.48 Even so, it seems clear that ifthere is a relationship between democracy and growth, it is more likelyto be perceptible in a cross-case setting. The positive hypothesis, as wellas the null hypothesis, is better approached in a sample rather than in acase.

47 Znaniecki (1934). See also the discussion in Robinson (1951).48 Kittel (1999, 2005); Kittel and Winner (2005); Levine and Renelt (1992); Temple

(1999).



Useful Variation: Rare versus Common

When analyzing causal relationships, we must be concerned not only withthe strength of an X/Y relationship but also with the distribution of evi-dence across available cases. Specifically, we must be concerned with thedistribution of useful variation – understood as variation (temporal orspatial) on relevant parameters that might yield clues about a causal rela-tionship. It follows that where useful variation is rare – that is, limitedto a few cases – the case study format recommends itself. Where, on theother hand, useful variation is common, a cross-case method of analysismay be more defensible.

Consider a phenomenon like social revolution, an outcome that occursvery rarely. The empirical distribution on this variable, if we count eachcountry-year as an observation, consists of thousands of nonrevolutionsand just a few revolutions. Intuitively, it seems clear that the few “revolu-tionary” cases are of great interest. We need to know as much as possibleabout them, for they exemplify all the variation that we have at our dis-posal. In this circumstance, a case study mode of analysis is difficult toavoid, though it might be combined with a large-N cross-case analysis. Asit happens, many outcomes of interest to social scientists are quite rare,so the issue is by no means trivial.49

By way of contrast, consider a phenomenon like turnover, understoodas a situation where a ruling party or coalition is voted out of office.Turnover occurs within most democratic countries on a regular basis, sothe distribution of observations on this variable (incumbency/turnover)is relatively even across the universe of country-years. There are lotsof instances of both outcomes. Under these circumstances a cross-caseresearch design seems plausible, for the variation across cases is evenlydistributed.

Another sort of variation concerns that which might occur within agiven case. Suppose that only one or two cases within a large popula-tion exhibit quasi-experimental qualities: the factor of special interest (X)

49 Consider the following topics and their – extremely rare – instances of variation: earlyindustrialization (England, the Netherlands); fascism (Germany, Italy); the use of nuclearweapons (United States); world war (World War I, World War II); single nontransferablevote electoral systems (Jordan, Taiwan, Vanuatu, pre-reform Japan); electoral systemreforms within established democracies (France, Italy, Japan, New Zealand, Thailand).The problem of “rareness” is less common where parameters are scalar rather thandichotomous. But there are still plenty of examples of phenomena whose distributionsare skewed by a few outliers, e.g., population (China, India); personal wealth (Bill Gates,Warren Buffett); ethnic heterogeneity (Papua New Guinea).



varies, and there is no corresponding change in other factors that mightaffect the outcome. (The quasi-experimental qualities of the case may bethe result of a manipulated treatment or a treatment that occurs naturally.These issues are explored in Chapter Six.) Clearly, we are likely to learn agreat deal from studying this particular case – perhaps a lot more than wemight learn from studying hundreds of additional cases that deviate fromthe experimental ideal. But again, if many cases have this experimentalquality, there is little point in restricting ourselves to a single example; across-case research design may be justified.

A final sort of variation concerns the characteristics exhibited by a caserelative to a particular theory that is under investigation. Suppose that acase provides a “crucial” test for a theory: it fits that theory’s predictionsso perfectly and so precisely that no other explanation could plausiblyaccount for the performance of the case. If no other crucial cases presentthemselves, then an intensive study of this particular case is de rigueur.Of course, if many such cases lie within the population, then it may bepossible to study them all at once (with some sort of numeric reductionof the relevant parameters).

The general point here is that the distribution of useful variation acrossa population of cases matters a great deal in the choice between case studyand cross-case research designs. (Many of the issues discussed in ChaptersFive and Six are relevant to this discussion of what constitutes “usefulvariation.” Thus, I have touched upon these issues only briefly in thissection.)

Data Availability

I have left the most prosaic factor for last. Sometimes, one’s choice ofresearch design is driven by the quality and quantity of information thatis currently available, or could easily be gathered, on a given question.This is a practical matter and is separate from the actual shape of theempirical universe. It concerns, rather, what we know about the formerat a given point in time.50 The question of evidence may be posed asfollows: how much do we know about the cases at hand that mightbe relevant to the causal question of interest, and how precise, certain,and case-comparable is that data? An evidence-rich environment is onewhere all relevant factors are measurable, where these measurements are

50 Of course, what we know about the potential cases is not independent of the underlyingreality; it is, nonetheless, not entirely dependent on that reality.



relatively precise, where they are rendered in comparable terms acrosscases, and where one can be relatively confident that the information isindeed accurate. An evidence-poor environment is the opposite.

The question of available evidence impinges upon choices in researchdesign when one considers its distribution across a population of cases. Ifrelevant information is concentrated in a single case, or if it is contained inincommensurable formats across a population of cases, then a case studymode of analysis is almost unavoidable. But if it is evenly distributedacross the population – that is, if we are equally well-informed aboutall cases – and is case-comparable, then there is little to recommend anarrow focus. (I employ data, evidence, and information as synonyms inthis section.)

Consider the simplest sort of example, where information is truly lim-ited to one or a few cases. Accurate historical data on infant mortal-ity and other indices of human development are currently available foronly a handful of countries (these include Chile, Egypt, India, Jamaica,Mauritius, Sri Lanka, the United States, and several European coun-tries).51 This data problem is not likely to be rectified in future years,as it is exceedingly difficult to measure infant mortality except by publicor private records. Consequently, anyone studying this general subject islikely to rely heavily on these cases, where in-depth analysis is possibleand profitable. Indeed, it is not clear whether any large-N cross-case anal-ysis is possible prior to the twentieth century. Here, a case study formatis virtually prescribed, and a cross-case format proscribed.

Other problems of evidence are more subtle. Let us dwell for themoment on the question of data comparability. In their study of socialsecurity spending, Mulligan, Gil, and Sala-i-Martin note that

although our spending and design numbers are of good quality, there are somemissing observations and, even with all the observations, it is difficult to reducethe variety of elderly subsidies to one or two numbers. For this reason, case studiesare an important part of our analysis, since those studies do not require numbersthat are comparable across a large number of countries. Our case study analysisutilizes data from a variety of country-specific sources, so we do not have to reduce‘social security’ or ‘democracy’ to one single number.52

Here, the incommensurability of the evidence militates in favor of a casestudy format. In the event that the authors (or subsequent analysts) dis-cover a coding system that provides reasonably valid cross-case measures

51 Gerring (2006c).52 Mulligan, Gil, Sala-i-Martin (2002: 13).



of social security, democracy, and other relevant concepts, then our stateof knowledge about the subject is changed, and a cross-case researchdesign is rendered more plausible.

Importantly, the state of evidence on a topic is never entirely fixed.Investigators may gather additional data, recode existing data, or discovernew repositories of data. Thus, when discussing the question of evidence,one must consider the quality and quantity of evidence that could begathered on a given question, given sufficient time and resources. Here itis appropriate to observe that collecting new data, and correcting existingdata, is usually easier in a case study format than in a large-N cross-caseformat. It will be difficult to rectify data problems if one’s cases numberin the hundreds or thousands. There are simply too many data points toallow for this.

One might consider this issue in the context of recent work on democ-racy. There is general skepticism among scholars with respect to theviability of extant global indicators intended to capture this complexconcept (e.g., the data gathered by Freedom House and by the Politydataset).53 Measurement error, aggregation problems, and questions ofconceptual validity are rampant. When dealing with a single country ora single continent, it is possible to overcome some of these faults by man-ually recoding the countries of interest.54 The case study format oftengives the researcher an opportunity to fact check, to consult multiplesources, to go back to primary materials, and to overcome whatever biasesmay affect the secondary literature. Needless to say, this is not a feasi-ble approach for an individual investigator if one’s project encompassesevery country in the world. The best one can usually manage, under thecircumstances, is some form of convergent validation (by which differ-ent indices of the same concept are compared) or small adjustments inthe coding intended to correct for aggregation problems or measurementerror.55

For the same reason, the collection of original data is typically moredifficult in cross-case analysis than in case study analysis, involving greaterexpense, greater difficulties in identifying and coding cases, learning for-eign languages, traveling, and so forth. Whatever can be done for a set ofcases can usually be done more easily for a single case.

53 Bollen (1993); Bowman, Lehoucq, and Mahoney (2005); Munck and Verkuilen (2002);Treier and Jackman (2005).

54 Bowman, Lehoucq, and Mahoney (2005).55 Bollen (1993); Treier and Jackman (2005).



It should be kept in mind that many of the countries of concern toanthropologists, economists, historians, political scientists, and sociolo-gists are still terra incognita. Outside the OECD, and with the exceptionof a few large countries that have received careful attention from scholars(e.g., India, Brazil, China), most countries of the world are not well cov-ered by the social science literature. Any statement that one might wish tomake about, say, Botswana will be difficult to verify if one has recourseonly to secondary materials. And these – very limited – secondary sourcesare not necessarily of the most reliable sort. Thus, if one wishes to saysomething about political patterns obtaining in roughly 90 percent ofthe world’s countries, and if one wishes to go beyond matters that canbe captured in standard statistics collected by the World Bank and theIMF and other agencies (and these can also be very sketchy when lesser-studied countries are concerned), one is more or less obliged to conduct acase study. Of course, one could, in principle, gather similar informationacross all relevant cases. However, such an enterprise faces formidablelogistical difficulties. Thus, for practical reasons, case studies are some-times the most defensible alternative when the researcher is faced with aninformation-poor environment.

However, this point is easily turned on its head. Datasets are nowavailable to study many problems of concern to the social sciences. Thus,it may not be necessary to collect original information for one’s book,article, or dissertation. Sometimes in-depth single-case analysis is moretime-consuming than cross-case analysis. If so, there is no informationaladvantage to a case study format. Indeed, it may be easier to utilize exist-ing information for a cross-case analysis, particularly when a case studyformat imposes hurdles of its own – travel to distant climes, risk of per-sonal injury, expense, and so forth. It is interesting to note that someobservers consider case studies to be “relatively more expensive in timeand resources.”56

Whatever the specific logistical hurdles, it is a general truth that theshape of the evidence – that which is currently available and that whichmight feasibly be collected by an author – often has a strong influenceon an investigator’s choice of research design. Where the evidence forparticular cases is richer and more accurate, there is a strong prima facieargument for a case study format focused on those cases. Where, bycontrast, the relevant evidence is equally good for all potential cases, and is

56 Stoecker (1991: 91).



comparable across those cases, there is no reason to shy away from cross-case analysis. Indeed, there may be little to gain from case study formats.

Causal Complexity

Not all factors that impinge upon the choice of research designs haveclear affinities to case study or cross-case study research. Others are inde-terminate in their implications. Whether these factors favor the focusedanalysis of a few cases or a relatively superficial analysis of many casesdepends upon issues that are difficult to generalize about.

Let us begin with the vexed question of causal complexity. Case studyresearchers often laud their favored method for its better grasp of com-plex causes,57 while critics claim that the more complex the causal rela-tionship, the more necessary is cross-case evidence.58 Intuitively, bothpositions seem plausible, and much evidently depends upon the interpre-tation of “complexity,” which might refer to probabilistic (rather thaninvariant) causal patterns, necessary and/or sufficient causes, nonlinearrelationships, multiple causes (“equifinality”), nonadditive causal inter-relationships, causal sequences (where causal order affects the outcomeof interest), a large number of plausible causes (the problem of overde-termination), and many other things besides. Indeed, “complexity,” asthe term is used in social science circles, seems to refer to any feature ofa causal problem that does not fit snugly with standard assumptions oflinearity, additivity, and independence. As such, it is a red herring, for ithas no determinate meaning.

Some kinds of causal complexity, like necessary and sufficient condi-tions, may militate in favor of a case study research design, as arguedearlier in this chapter (see the section on causal strength). Others, I willargue, are indeterminate. That is, sometimes complex causal relationshipsare rendered visible in case study research, and we are able to parse outthe independent causal effects of each factor (which may depend on theirposition in an extended causal chain). This is what case study researchdoes, if it is done well and if the chosen case is amenable to that style ofresearch. But oftentimes, this is simply not feasible. Similarly, sometimesone is able to model complex causal relationships in a cross-case setting,and sometimes not. In short, it all depends.

57 Abbott (1990); George and Bennett (2005); Ragin (1987: 54; 2000: Chapter 4);Rueschemeyer (2003).

58 Goldthorpe (1997); King, Keohane, and Verba (1994); Lieberson (1985).



Let us explore an example. Suppose one is interested in the influenceof fiscal pressures on social revolution – the idea that as governmentsget more strapped for cash, they are likely to seek to raise taxes, which,in turn, may spark revolt. A nice (confirming) case study would showprecisely that, without any interfering (confounding) factors. It would beeventful, in a quasi-experimental way (see Chapter Six). An intervention(treatment) would occur – increasing budget deficits, followed by increas-ing taxes – and the result could be observed. However, a bad (confirming)case would show that lots of things were happening at the same time thatcould also have caused revolution. As it happens, lots of things do tendto happen together during critical junctures like revolutions, and so it isoften quite difficult to tease out real and spurious causal effects. In sta-tistical terms, this may be understood as a problem of collinearity. Now,let us suppose that you have at your disposal 100 countries, with annualmeasurements of fiscal pressure, tax instruments, as well as various con-founders (controls). Collinearity is still a formidable problem. But with agreat deal of cross-case evidence, there is at least a fighting chance that itcan be overcome, while there is little chance of overcoming it in most casestudy settings. (Indeed, some statisticians have looked upon the problemof collinearity as a problem of data insufficiency.)

The general point remains. “Complexity,” by itself (keeping in mindthat complexity can mean many things), does not favor either a case studyor a cross-case approach to causal analysis.

The State of the Field

Another sort of contextual consideration concerns the state of researchon a given topic within a field. Social scientists are accustomed to the ideathat research occurs within the context of an ongoing tradition. All workis dependent for the identification of topic, argument, and evidence on thisresearch tradition. What we need to know, and hence ought to study, is tosome extent contingent upon what is already known. It follows from thisthat the utility of case study research relative to non–case study researchis to some extent the product of the state of research within a given field.A field dominated by case studies may have little need for another casestudy. A field where cross-case studies are hegemonic may be desperatelyin need of in-depth studies focused on understudied cases.

Indeed, much of the debate over the utility of the case study method haslittle to do with the method itself and more to do with the state of currentresearch in a particular field. If both case study and cross-case methods



have much to recommend them (an implicit assumption of this book),then both ought to be pursued – perhaps not in equal measure, but atleast with equal diligence and respect. There is no virtue, and potentiallygreat harm, in pursuing one approach to the exclusion of the other, or inghettoizing the practitioners of the minority approach. The triangulationessential to social scientific advance demands the employment of a varietyof (viable) methods, including the case study. But there is little that wecan say about this desideratum in general, since it depends on the shapeof an individual field or subfield.


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part ii

DOING CASE STUDIES

In the opening pages of this book, I highlighted the rather severe disjunc-ture that has opened up between an often-maligned methodology and aheavily practiced method. The case study is disrespected, but nonethelessregularly employed. Indeed, it remains the workhorse of most disciplinesand subfields in the social sciences, as demonstrated in Chapter One.How, then, can one make sense of this discrepancy between methodolog-ical theory and methodological praxis? This was the question animatingPart One of the book.

The torment of the case study begins with its definitional penumbra,as described in Chapter Two. Frequently, this key term is conflated with adisparate set of methodological traits that are not definitionally entailed.Our first task, therefore, was to craft a narrower and more useful conceptfor purposes of methodological discussion. The case study, I argued, is bestdefined as an intensive study of a single case (or a small set of cases) withan aim to generalize across a larger set of cases of the same general type.If the inference pertains to nation-states, then a case study would focuson one or several nation-states (while a cross-case study would focus onmany nation-states at once). If the inference pertains to individuals, thena case study would focus on one or several individuals (while a cross-casestudy would focus on many individuals at once). And so forth.

It follows from this definition that case studies may be small- or large-N(since a single case may provide few or many observations), qualitative orquantitative, experimental or observational, synchronic or diachronic. Italso follows that the case study research design comports with any macro-theoretical framework or paradigm – for example, behavioralism, ratio-nal choice, institutionalism, or interpretivism. It is not epistemologically

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66 II. Doing Case Studies

distinct.1 What differentiates the case study from the cross-case study issimply its way of defining observations, not its analysis of those observa-tions or its method of modeling causal relations. The case study researchdesign constructs its observations from a single case or a small numberof cases, while cross-case research designs construct observations acrossmultiple cases. Cross-case and case study research operate, for the mostpart, at different levels of analysis.

In other respects, the predicament of the case study is not merely def-initional but inheres in the method itself. To study a single case withintent to shed light upon other cases brings in its train several method-ological ambiguities. First, the concept of a case study is dependent uponthe particular proposition that one has in mind, a proposition that maychange through time (as the study is digested by the academic commu-nity) or even within a given study (as the author changes her level ofanalysis). Second, the boundaries of a case are sometimes – despite theresearcher’s best efforts – open-ended. This is particularly true of temporalboundaries, which may extend into the future and into the past in ratherindefinite ways. Third, case studies usually build upon a variety of covari-ational evidence; there is no single type of case study, but rather five (seeTable 2.4).

The travails of the case study are rooted, additionally, in an insufficientappreciation of the methodological trade-offs that this method calls forth,as discussed in Chapter Three. At least eight characteristic strengths andweaknesses must be considered (see Table 3.1). Ceteris paribus, case stud-ies are more useful when the purpose of research is hypothesis generatingrather than hypothesis testing, when internal validity is given preferenceover external validity, when insight into causal mechanisms is prioritizedover insight into causal effects, when propositional depth is prized overbreadth, when the population is heterogeneous rather than homogeneous,when causal relationships are strong rather than weak, when useful vari-ation on key parameters is rare rather than commonplace, and whengood-quality evidence is concentrated rather than dispersed. Causal com-plexity and the existing state of a field of research may also influence aresearcher’s choice to adopt a single-case or cross-case research design,though their methodological implications are equivocal.

The objective of the first section of the book was to restore a sense ofmeaning, purpose, and integrity to the case study method. It is hoped that

1 Epistemological differences between case study and cross-case work are a theme in Orum,Feagin, and Sjoberg (1991: 22).


II. Doing Case Studies 67

by offering a more carefully bounded definition of the method it might berescued from some of its ambiguities. It is also hoped that the characteristicstrengths of this method, as well as its limitations, will be more apparentto producers and consumers of case study research. The case study is auseful tool for some research objectives and in some research settings, butnot all.

In the second section of the book, I turn to practical questions ofresearch design. How does one employ the intensive study of a singlecase, or a small number of cases, to shed light on a broader class of cases?

Chapter Four addresses preliminary issues pertaining to this quest.Chapter Five examines the problem of case selection. Chapter Six exam-ines the problem of internal validity through the prism of experimentalresearch designs. Chapter Seven approaches the problem of internal valid-ity through the use of a rather different approach called process tracing.The epilogue addresses research design elements of single-outcome stud-ies – where a single outcome, rather than a broader class of outcomes, isof primary interest.


4

Preliminaries

Before entering into a discussion of specific research design techniques,it is important to insert a preliminary discussion of several factors thatovershadow all research design issues in case study work. These includeevidence-gathering techniques, the formulation of a hypothesis, degrees offalsifiability, the tension between particularizing and generalizing objec-tives in a case study, the identification of a population that the casestudy purports to represent, and the importance of cross-level research.Although these six issues affect all empirical work in the social sciences,they are particularly confusing in the context of case study work, andconsequently merit our close attention.

The Evidence

The case study, I argued in Chapter Two, should not be defined bya distinctive method of data collection but rather by the goals of theresearch relative to the scope of the research terrain. Evidence for a casestudy may be drawn from an existing dataset or set of texts or maybe the product of original research by the investigator. Written sourcesmay be primary or secondary. Evidence may be quantitative, qualita-tive, or a mixture of both – as when qualitative observations are codednumerically so as to create a quantitative variable.1 Evidence may bedrawn from experiments (discussed in Chapter Six), from “ethnographic”

1 Kritzer (1996); Stoker (2003); Theiss-Morse et al. (1991).

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Preliminaries 69

field research,2 from unstructured interviews, or from highly structuredsurveys.3

In short, there are many ways to collect evidence (“data”), and noneof these methods is unique to the case study. Techniques differ greatlyfrom discipline to discipline, subfield to subfield, and topic to topic – andrightly so. To be sure, the more intensive the evidence-gathering method,the more difficult it will be to implement that technique across multiplecases. In this respect, ethnographic research is rightly identified as a casestudy method. Even so, there is no theoretical limit to the number ofethnographies that may be conducted by an individual, or by a group ofindividuals (perhaps working on a subject over several generations). Oncethat number has extended beyond the point where qualitative analysis ispossible, some form of mathematical reduction is more or less required ifan integrative approach to the population is desired. Where, for example,a great deal of textual data exists, analysts usually have recourse to contentor discourse analysis.4

Getting the facts right is essential to doing good case study research.However, since the methods of data collection are legion, there is littlethat one can say, in general, about this problem.5

One issue deserves emphasis, however. All data requires interpretation,and in this respect all techniques of evidence gathering are interpretive.6

2 The literature on ethnography (including participant observation and field research) isimmense. For a brief discussion of early work in this genre, see Hamel (1993). Contem-porary works in the social sciences include Becker (1958); Burawoy, Gamson, and Bur-ton (1991); Denzin and Lincoln (2000); Emerson (1981, 2001); Fenno (1978: 249–93;1986; 1990); Hammersley and Atkinson (1983); Jessor, Colby, and Shweder (1996); Pat-ton (2002: 339–428); and Smith and Kornblum (1989). The technique known as eth-nomethodology is laid out in Garfinkel (1967). Helper (2000) discusses the potentialof field research in economics. Examples of ethnographic research in the “hard science”fields of criminology, medical science, and psychology include Athens (1997); Bosk (1981);Estroff (1985); and Katz (1999) – all cited in Rosenbaum (2004: 3). Practical advice onthe conduct of field research, with special attention to foreign locations, can be found inBarrett and Cason (1997) and Lieberman, Howard, and Lynch (2004).

3 A general introduction to survey research is provided by Dillman (1994). Gubrium andHolstein (2002) offers a comprehensive treatment of interview research.

4 Discussion of various techniques can be found in Coulthard (1992); Hart (1997); Krip-pendorff (2003); Laver et al. (2003); Neuendorf (2001); Phillips and Hardy (2002 ); andSilverman (2001). See also “Symposium: Discourse, Content Analysis” (2004).

5 For research on primary and secondary documents, see Thies (2002). See also Bloch(1941/1953); Elton (1970); George and Bennett (2005); Lustick (1996); Thompson(1978); Trachtenberg (2005); and Winks (1969).

6 Interpretivist (a.k.a. hermeneutic or Verstehen) methods refer broadly to evidence-gathering techniques that are focused on the intentions and subjective meanings contained



Rarely, if ever, does the evidence speak for itself. There may be such thingsas “brute facts” – for example, Caesar crossed the Rubicon in 51b.c.7

However, in a study oriented toward the discovery of general causes oneis required to invest such acts with meaning. And this requires judgmenton the part of the investigator.

Note that the social sciences are defined by their focus on decisionalbehavior – actions by human beings and humanly created institutions thatare not biologically programmed. Thus, any social scientific explanationinvolves assumptions about why people do what they do or think whatthey think, a matter of intentions and motivations. Social science is, ofnecessity, an interpretive act.

In many settings, actor-centered meanings are more or less self-evident.When people behave in apparently self-interested ways, the researchermay not feel compelled to investigate the intentions of the actors.8 Buy-ing low and selling high is intentional behavior, but it probably does notrequire detailed ethnographic research in situations where we know (orcan intuit) what is going on. On the other hand, if one is interested in whymarkets work differently in different cultural contexts, or why persons insome cultures give away their accumulated goods, or why in some othercircumstances people do not buy low and sell high (when it would appearto be in their interest to do so), one is obliged to move beyond read-ily apprehensible (“obvious”) motivations such as self-interest.9 In thesesituations – encompassing many of the events that social scientists haveinterested themselves in – careful attention to meaning, as understood bythe actors themselves, is essential.10 Howard Becker explains:

To understand an individual’s behaviour, we must know how he perceives thesituation, the obstacles he believed he had to face, the alternatives he saw

in social actions. See Gadamer (1975); Geertz (1973, 1979a, 1979b); Gibbons (1987);Hirsch (1967); Hirschman (1970); Hoy (1982); MacIntyre (1971); Rabinow and Sullivan(1979); Taylor (1985); von Wright (1971); Winch (1958); and Yanow and Schwartz-Shea(2006).

7 The term originates with Anscombe (1958), though her usage is somewhat different frommy own. For a similar use of the term, see Neta (2004).

8 To be sure, self-interested behavior (beyond the level of self-preservation) is also, on somelevel, socially constructed. Yet if we are interested in understanding the effect of pocket-book voting on election outcomes, there is little to be gained by investigating the originsof money and material goods as a motivating force in human behavior. Some things wecan afford to take for granted. For a useful discussion, see Abrami and Woodruff (2004).

9 Geertz (1978).10 Davidson (1963); Ferejohn (2004); Rabinow and Sullivan (1979); Stoker (2003); Taylor

(1970).


Preliminaries 71

opening up to him. We cannot understand the effects of the range of possibil-ities, delinquent subcultures, social norms and other explanations of behaviourwhich are commonly invoked, unless we consider them from the actor’s point ofview.11

This is the interpretivist’s quest – to understand behavior from the actor’spoint of view – and it is an enlightening quest wherever the actor’s pointof view does not correspond to common sense.

Thus, evidence in a social-scientific study often involves an act of inter-pretation. But this is not unique, or even distinct, to the case study format.

The Hypothesis

It is impossible to pose questions of research design until one has at leasta general idea of what one’s research question is. There is no such thing ascase selection or case analysis in the abstract. A research design must havea purpose, and that purpose is defined by the inference that it is intendedto demonstrate or prove.

In this book I am concerned primarily with causal inference, rather thaninferences that are descriptive or predictive in nature. Thus, all hypothesesinvolve at least one independent variable (X) and one dependent variable(Y). For convenience, I shall label the causal factor of special theoreticalinterest X1, and the control (background) variable, or vector of controls(if there are any), X2.

If a writer is concerned to explain a puzzling outcome, but has nopreconceptions about its causes, then the research will be described asY-centered. If a researcher is concerned to investigate the effects of aparticular cause, with no preconceptions about what these effects mightbe, the research will be described as X-centered. If a researcher is con-cerned to investigate a particular causal relationship, the research will bedescribed as X1/Y-centered, for it connects a particular cause with a par-ticular outcome.12 X- or Y-centered research is exploratory; its purposeis to generate new hypotheses. X1/Y-centered research, by contrast, isconfirmatory/disconfirmatory; its purpose is to test an existing hypothesis.

Note that to pursue an X1/Y-centered analysis does not imply that thewriter is attempting to prove or disprove a monocausal or deterministic

11 Becker (1970: 64), quoted in Hamel (1993: 17).12 This expands on Mill (1843/1872: 253), who wrote of scientific inquiry as twofold:

“either inquiries into the cause of a given effect or into the effects or properties of a givencause.”



argument. The presumed causal relationship between X1 and Y may beof any sort. X1 may explain only a small amount of variation in Y. TheX1/Y relationship may be probabilistic. X1 may refer either to a singlevariable or to a vector of causal factors. This vector may be an interre-lationship (e.g., an interaction term). The only distinguishing feature ofX1/Y-centered analysis is that a specific causal factor(s), a specific out-come, and some pattern of association between the two are stipulated.Thus, X1/Y-centered analysis presumes a particular hypothesis – a propo-sition. Y- or X-centered analysis, by contrast, is much more open-ended.Here, one is “soaking and poking” for causes or effects.13 Invoking acontrast that was introduced in Chapter Three, we may say that Y- orX-centered analysis is hypothesis-generating, while X1/Y-centered analy-sis is hypothesis-testing.

As a rule, the more specific and operational a causal hypothesis is, theeasier it will be to identify a set of relevant cases. Naturally, the researcher’soperating hypothesis may change in the course of her research. Indeed, theexploratory nature of much case-based research is one of the strengths ofthis research design, as observed in Chapter Three. It would be a mistaketo suppose that hypotheses can be immaculately conceived, in isolationfrom the contaminating influences of the data. This piece of positivistdogma we would do well to forget. It is often preached, but rarely prac-ticed – and, when practiced, rarely to good effect. Usually, a hypothesisarises from an open-ended conversation between a researcher and her evi-dence. Indeed, one may have only a rough idea of an argument until onehas carried out considerable research. Social scientific study is often moti-vated by a suspicion – the researcher’s qualified hunch – that something“funny” is going on here or there. Puzzles are good points of departure.Even so, issues of research design cannot be fully addressed until thatinitial hunch is formulated as a specific hypothesis.

A quick glance at the real world of social science reveals that few studiesare innocently Y- or X-centered. Researchers usually have some presup-positions about what causes Y or about what X causes. In most circum-stances, the researcher is well advised to strive for a more fully elaboratedhypothesis, one that encompasses both sides of the causal equation. Y-and X-centered analyses are problematic points of departure. They arehard to pin down precisely because one side of the causal equation isopen-ended.

13 Fenno (1978).


Preliminaries 73

Recall, also, that the testing of a single hypothesis (yours or someoneelse’s) cannot be conducted in isolation. There are always competitors,even if these competing theories are difficult to identify. (You may have toconstruct them yourself if the field of inquiry is relatively undeveloped.)A good research design is one that distinguishes the effects of one causalfactor from others that might have contributed to a result. If the theoryat issue is broader than a single, obvious causal factor (if it can be oper-ationalized in a variety of ways), then a good research design is one thatconfirms that theory, while disconfirming others – or at least showingthat they cannot account for a specific set of results.14 A good researchdesign eliminates rival explanations. Thus, in thinking through issues ofresearch design, it is helpful to ask oneself the following question: is therean alternative way to explain this set of outcomes?

Finally, one must keep in mind that all causal arguments presume acausal mechanism, or a set of mechanisms.15 A mechanism is that whichexplains the putative relationship between X1 and Y. It is the causal path-way, or connecting thread, between X1 and Y. A specific and determinatecausal pathway is the smoking gun of causal analysis. Of course, causalpathways in social research are usually considerably more ambiguous thanthe smoking gun metaphor suggests. This is why research designs oftenfocus on this difficult, but essential, task. That is to say, in testing rivaltheories one is also, necessarily, testing rival causal mechanisms, not justthe covariational pattern between X1 and Y. Indeed, we have observedthat one of the strengths of the case study is that it often sheds light oncausal mechanisms that remain obscure in cross-case analysis (ChapterThree).

Thus, in thinking through research design issues, it is helpful to askoneself what causal mechanisms a theory stipulates, and whether theyare multiple, conjunctural, or take some other complex form. If you areresearching in an exploratory mode these same questions must be asked,though in a more open-ended fashion. In either case, evidence drawn

14 Testing really big, abstract theories such as deterrence and realism (both from the politicalscience subfield of international relations) is much more complicated than testing specifichypotheses. The main problem is that macro-theories (a.k.a. frameworks, paradigms) canbe operationalized in so many different ways. They are, therefore, difficult to falsify –or, for that matter, to confirm. In this book I am interested only in the testing of fairlyspecific hypotheses.

15 Granted, it is possible to make a strong argument for a causal relationship on the basis ofcovariational evidence alone, particularly if the covariational evidence is experimental.However, that argument will be even stronger if the researcher can also specify a causalmechanism. For further discussion, see Chapter 3.



from the case study should be enlisted to prove, or disprove, the theoryat hand. That is, predictions or expectations about causal mechanismsmay influence the choice of cases to be studied. “Black boxes” should bereplaced with “smoking guns,” wherever possible.

Degrees of Falsifiability

Karl Popper sought to classify all scientific propositions according to theirdegree of falsifiability – that is, the ease with which a proposition could beproven false.16 This, in turn, may be thought of as a matter of “riskiness.”A risky proposition is one that issues multiple precise and determinateempirical predictions, predictions that could not easily be explained byother causal factors (external to the theory of interest) and hence may beinterpreted as strong corroborating evidence for the theory at hand.

Falsifiability/riskiness will be discussed in greater detail in the follow-ing chapter. For the moment, let us observe that there is a wide range ofvariation on this dimension. Some case studies generate (or test) proposi-tions that are highly risky. Others are pitched in such abstract or ambigu-ous terms that they can hardly fail when tested against a larger popula-tion of cases (other than the case under intensive study). For example,E. P. Thompson’s renowned history The Making of the English WorkingClass (1963) provides a case study of class formation in one national set-ting (England). This suggests a very general purview, perhaps applicableto all countries in the modern era. Thompson does not offer a specific the-ory of class formation, aside from the rather hazy notion that the workingclass participates in its own development. Thus, unless we intuit a greatdeal (creating a general theory where there is only a suggestion of one), wecan derive relatively little that might be applicable to a broader populationof cases.

Many case studies examine a loosely defined general topic – war, revo-lution, gender relations – in a particular setting. Indeed, the narrowest ter-rains sometimes claim the broadest extensions. Studies of a war are studiesof war; studies of a farming community are studies of farming commu-nities everywhere; studies of individuals are studies of leadership or ofhuman nature, and so forth. But such studies may refrain from adoptinggeneral theories of war, farming, leadership, or human nature. Thiswould be true, for example, of most case study work in the interpretivist

16 Popper (1934/1968; 1963).


Preliminaries 75

tradition.17 Similarly, case studies that carry titles like “Ideas Matter,”“Institutions Matter,” or “Politics Matters” do not generally culminatein risky predictions. They tell us about an instance in which ideas mattered(“ideas mattered here”), but do not produce generalizable propositionsabout the role of ideas. Most work based on the organizing tool of criticaljunctures and path-dependent sequences is also of this nature, since thepath in question is unique while the fact of its being a path applies, in somevery general sense, across cases.18 What all these theoretical frameworkshave in common (indeed, about the only thing they have in common) isthat they are both broad and vague. They offer a framework which maybe used to shed light on a particular case, but not a falsifiable propositionthat could be applied to other cases.

By contrast, some case study work moves beyond the analysis ofambiguous causal frameworks to specific propositions. X1 is said to causeY across some range of cases and with some set of background conditions.A good example is Ben Reilly’s study of the role of electoral systems in eth-nically divided societies. Reilly argues, on the basis of several case studies,that single-transferable-vote (STV) electoral systems have a moderatingeffect on group conflict relative to first-past-the-post (FPP) electoral sys-tems.19 This sort of case study is risky insofar as it proposes a specificcausal hypothesis that can be tested – and potentially falsified – across abroader range of cases.20

17 Clifford Geertz (1973: 26), echoing the suspicion of most historians and anthropologists –of all those, presumably, who hold an interpretivist view of the social scienceenterprise – describes generalizing across cases as clinical inference. “Rather than begin-ning with a set of observations, attempting to subsume them under a governing law, suchinference begins with a set of (presumptive) signifiers, attempts to place them within anintelligible frame. Measures are matched to theoretical predictions, but symptoms (evenwhen they are measured) are scanned for theoretical peculiarities – that is, they are diag-nosed.” For a brief overview of interpretivism, see Gerring (2004a). This genre of casestudy may be referred to as interpretivist, idiographic, or “contrast of contexts” (Skocpoland Somers 1980).

18 Collier and Collier (1991/2002); Pierson (2000, 2004).19 Reilly (2001). For other examples see Eaton (2003); Elman (1997); Lijphart (1968); and

Stratmann and Baur (2002). This is the style of case study analysis associated with DavidCollier (1993); Harry Eckstein (1975); Alexander George and Andrew Bennett (Georgeand Bennett 2005; George and Smoke 1974); Arend Lijphart (1975); Skocpol and Somers(1980); and Robert Yin (1994). It is probably the dominant style in economics, politicalscience, and sociology.

20 Arguably, case studies are riskier than cross-case studies if, and insofar as, a theory isgenerated in the absence of knowledge about a broader set of cases. In this respect, casestudy work is commendable, from a Popperian perspective. However, I don’t advise thissort of “blind” case study work, and doubt that it ever really occurs.



The Particular and the General

I have stipulated that the concept of a case study is, at least to some extent,generalizing. A case study, strictly speaking, must generalize across a setof cases (see Chapter Two).21 However, the breadth of an inference isobviously a matter of many degrees. No case study (so-called) denies theimportance of the case under special focus, and no case study forswearsthe generalizing impulse altogether. So the particularizing/generalizing dis-tinction is rightly understood as a continuum, not a dichotomy. Case stud-ies typically partake of both worlds. They are studies both of somethingparticular and of something more general.

This tension is apparent in Graham Allison’s well-known study – whosesubtitle, Explaining the Cuban Missile Crisis, invokes a narrow topic,while the title, Essence of Decision, suggests a much larger topic (govern-ment decision making). Evidently, different propositions within this samework apply to different subjects, a complication that is noted explicitly bythe author. The particularizing/generalizing distinction helps to categorizedifferent studies or different moments within the same study.

Not surprisingly, one finds a good deal of disputation about the appro-priate scope of inferences generated by case study research. Jack Gold-stone argues that case studies are “aimed at providing explanations forparticular cases, or groups of similar cases, rather than at providing gen-eral hypotheses that apply uniformly to all cases in a suspected case-universe.”22 Alexander George and Richard Smoke advise the use ofcase studies for the formulation of what they call “contingent gener-alizations” – “if circumstances A then outcome O.”23 Like many casestudy researchers, they lean toward a style of analysis that investigatesdifferences across cases or across subtypes, rather than commonalities.Harry Eckstein, on the other hand, envisions case studies that confirm(or disconfirm) hypotheses as broad as those provided by cross-casestudies.24

Sometimes, the particularizing or generalizing quality of a case studyis driven by the concerns of the investigator. It is said that some ana-lysts would prefer to explain 90 percent of the variance in a single case,while others would rather explain 10 percent of the variance across

21 In French, the connotation is quite different. L’Analyse de cas is understood to mean asingle-event study, not a case study of some broader phenomenon.

22 Goldstone (1997: 108).23 George and Smoke (1974: 96). See also George and Bennett (2005: 30–1).24 Eckstein (1975).


Preliminaries 77

100 cases. There are lumpers (generalizers) and splitters (particularizers).Economists, political scientists, and sociologists are usually more inter-ested in generalizing than in particularizing, while anthropologists andhistorians are nowadays more interested in explaining particular con-texts. We have already discussed the trade-off between depth and breadth(Chapter Three).

The particularizing/generalizing tug-of-war is also conditioned by theshape of the empirical phenomena. With respect to the topic of socialmobility, John Goldthorpe and Robert Erikson note that while some pat-terns are well explained by cross-case (general) models, others are resistantto those general explanations.

Our analyses pointed . . . to the far greater importance of historically formedcultural or institutional features or political circumstances which could not beexpressed as variable values except in a quite artificial way. For example, levelsof social fluidity were not highly responsive to the overall degree of educationalinequality within nations, but patterns of fluidity did often reflect the distinctive,institutionally shaped character of such inequality in particular nations, such asGermany or Japan. Or again, fluidity was affected less by the presence of a statesocialist regime per se than by the significantly differing policies actually pursuedby the Polish, Hungarian or Czechoslovak regimes on such matters as the collec-tivization of agriculture or the recruitment of the intelligentsia. In such instances,then, it seemed to us that the retention of proper names and adjectives in ourexplanatory accounts was as unavoidable as it was desirable, and that little wasto be gained in seeking to bring such historically specific effects within the scopeof theory of any kind.25

This empirical field offers a good example of how a single phenomenon(social mobility) may exhibit features that are both uniform and uniqueacross the chosen cases.

Statistical researchers will be familiar with the technique of “fixedeffects,” which incorporate a unique intercept for each unit in a time-series cross-section model. This is another way of capturing the notionof diversity-within-uniformity – case specificity coexisting with casegenerality.

Case study research format generally occupies an in-between method-ological zone that is part “idiographic” and part “nomothetic” (I usethese terms with extreme circumspection, since they contain so many dif-ferent meanings). Some studies lean toward the former, others toward thelatter.

25 Goldthorpe (1997: 17).



Indeed, a degree of ambiguity is inherent in the enterprise of the casestudy. Avner Greif offers the following caveat at the conclusion of hisanalytic narrative of late medieval Genoa:

This study demonstrates the complexity of investigating self-enforcing politicalsystems. Such an investigation requires a detailed examination of the particulari-ties of the time and place under consideration, utilizing a coherent, context-specificmodel. Thus it may be premature to attempt to generalize based on this studyregarding the sources and implications of self-enforcing political systems.26

Here a researcher steeped in the nomothetic tradition of economics comesto terms with the fact that generalizations based on his own case studywork are highly speculative. It is not clear how far they might extend.27

Indeed, it is difficult to write a study of a single case that does not alsofunction as a case study, and vice versa. Nor is it always easy to neatlyseparate the single-case and cross-case components of a work. The reasonfor this structural ambiguity is that the utility of the case study rests on itsdouble function. One wishes to know both what is particular to that unitand what is general about it, and these elements are often unclear. Thus,in her study of multilateral economic sanctions, Lisa Martin confesses toher readers that

although I have chosen the cases to allow testing the hypotheses [of theoreticalinterest], other factors inevitably appear that seem to have had a significant influ-ence on cooperation in particular cases. Because few authors have focused on thequestion of cooperation in cases of economic sanctions, I devote some attention tothese factors when they arise, rather than keeping my analysis within the boundsof the hypotheses outlined in [the theory chapter].28

26 Greif (1998: 59). Weingast (1998: 153), in the same volume, notes that his case study“does not afford general tests on a series of other cases.” See also the introductory andconcluding chapters to this influential volume (Bates et al. 1998: 11, 231, 234). On theother hand, Levi elsewhere (1997: 6) insists that “analytic narrative combines detailedresearch of specific cases with a more general model capable of producing hypothesesabout a significant range of cases outside the sample of the particular project.”

27 George and Smoke (1974: 105) offer parallel reflections on their own case studies, focusedon deterrence in international relations. “These case studies are of twofold value. First,they provide an empirical base for the theoretical analysis. . . . But second, the case studiesare intended to stand in their own right as historical explanations of the outcomes ofmany of the major deterrence efforts of the Cold War period. They are ‘historical’ inthe sense that they are, of course, retrospective. However, they are also analytical in thesense that we employ a variety of tools, concepts in attempting to explain the reasonsbehind a particular outcome in terms of the inner logic of the deterrence process [a logicthat presumably extends across past, present and future]. They are therefore as much‘political science’ as they are ‘history.’ ”

28 Martin (1992: 97).


Preliminaries 79

It should be kept in mind that case studies often tackle subjects aboutwhich little was previously known or about which existing knowledge isfundamentally flawed. The case study typically presents original researchof some sort. Indeed, it is the opportunity to study a single case in greatdepth that constitutes one of the primary virtues of the case study method(see Chapter Three).

Consider that if a researcher were to restrict herself only to elements ofthe case that were generalizable (i.e., if she rigorously maintains a nomo-thetic mode of analysis), a reader might justifiably complain. Such rigorwould clarify the population of the primary inference, but it would alsoconstitute a considerable waste of scholarly energy. Imagine a study ofeconomic growth that focuses on Mauritius as a case study yet refusesto engage causal questions unless they are clearly applicable to othercountries (since this work is supposed to function as a case study of amore general phenomenon, growth). No mention of factors specific tothe Mauritian case is allowed; all proper nouns are converted into com-mon nouns.29 Imagine that the fruit of an anthropologist’s ten-year studyof a remote tribe, never heretofore visited, culminates in the analysis of aparticular causal relationship deemed to be generalizable, but at the costof ignoring all other features of tribal life in the resulting study. One canonly suppose that colleagues, mentors, and funding agencies would beunhappy with an ethnography so tightly focused on a general (cross-case)causal issue. Studies of the foregoing sort do not exist, because they areunduly general.

Since it is often difficult to tell which of the many features of a givencase are typical of a larger set of cases (and hence fodder for generalizableinferences) and which are particular to the case under study, the appro-priate expedient is for the writer to report all facts and hypotheses thatmight be relevant – in short, to overreport. Much of the detail providedby the typical case study may be regarded as “field notes” of plausibleutility for future researchers, perhaps having rather different agendas.

In sum, it seems justifiable for case studies to function on two lev-els simultaneously, the case itself and some broader class of (perhapsdifficult-to-specify) cases. The defining characteristic of the case studyis its ability to infer a larger whole from a much smaller part. Yet bothretain some importance in the final product. Thus, all case studies are to acertain extent betwixt and between. They partake of two worlds: they are

29 Przeworski and Teune (1970).



particularizing and generalizing. (Note that one portion of this book – theepilogue – is focused on work that is strongly particularizing, i.e., wherethe intent of the author is to elucidate a single outcome rather than a classof outcomes. Elsewhere, I am concerned primarily with the generalizingcomponent of case study research.)

Specifying a Population

Given the structural conflict between the two moments of the case study,it is absolutely crucial that case study writers be as clear as possibleabout which of their propositions are intended to describe the case underintensive investigation, and which are intended to apply to a broader setof cases. Each inference must have a clear breadth, domain, scope, orpopulation (terms that I use more or less interchangeably).

Regrettably, these matters are often left ambiguous. Studies focused onsome element of politics in the United States often frame their analysis asa study of politics – by implication, politics in general (everywhere andalways).30 One is left to wonder whether the study pertains only to Amer-ican politics, to all contemporary polities, or in varying degrees to both.Indeed, the slippage between study and case study may account for muchof the confusion that we encounter when reading single-case analyses.Ongoing controversies over the validity of Theda Skocpol’s analysis ofsocial revolution, Michael Porter’s analysis of industrial competitiveness,Alexander George and Richard Smoke’s study of deterrence failure, aswell as many other case-based studies, rest in part on the failure of theseauthors to clarify the scope of their inferences.31 It is not clear what thesestudies are about. At any rate, it is open to dispute. If, at the end of a study,the population of the primary inference remains ambiguous, so does thehypothesis. It is not falsifiable. Clarifying an inference may involve somesacrifice in narrative flow, but it is rightly regarded as the entry price ofsocial science.

Caution is evidently required when specifying the population of aninference. One does not wish to claim too much. Nor does one wish toclaim too little. Mistakes can be made in either direction, as we haveobserved. In this discussion I shall emphasize the virtues of breadth, forit is my impression that many case study researchers lean toward narrow

30 See e.g., Campbell et al. (1960).31 Skocpol (1979); Porter (1990); George and Smoke (1974). See also discussion in Collier

and Mahoney (1996); Geddes (1990); and King, Keohane, and Verba (1994).


Preliminaries 81

propositions – which seem more modest, more conservative – withoutrealizing the costs of doing so.

In discussion of two extraordinarily influential works of comparativehistory – Barrington Moore’s Social Origins of Dictatorship and Democ-racy and Theda Skocpol’s States and Social Revolutions – Skocpol andMargaret Somers declare that these studies, and others like them, “can-not be readily generalized beyond the cases actually discussed,” for theyare inductive rather than deductive exercises in causal analysis. Thus, anyattempt to project the arguments in these works onto future revolutions,or onto revolutions outside the class of specified outcomes, is foolhardy.The authors defend this limited scope by likening case-based research toa map. “No matter how good the maps were of, say, North America, thepilot could not use the same map to fly over other continents.”32

The map metaphor is apt for some phenomena, but not for others. Itbetrays the authors’ general assumption that most phenomena of interestto social science are highly variable across contexts, like the roadways andwaterways of a continent. Consider the causes of revolutions, as exploredby Skocpol in her path-breaking work. Skocpol carefully bounds her con-clusions, which are said to apply only to states that are wealthy and inde-pendent (through their history) of colonial rule – and hence exclude otherrevolutionary cases such as Mexico (1910), Bolivia (1952), and Cuba(1959).33 One’s willingness to accept this scope restriction is contingentupon accepting an important premise, namely, that the causes of revolu-tion in poor countries, or in countries with colonial legacies, are differentfrom the causes of revolution in other countries. One must accept theassumption of unit homogeneity among the chosen cases and unit hetero-geneity among the class of excluded cases. This is a plausible claim, but itis not beyond question. (Were the causes of revolution really so differentin Cuba and Russia?)

Evidently, the plausible scope of an argument depends on the particularargument and on judgments about various cases, inside and outside of theproposed population. When a researcher restricts an inference to a smallpopulation of cases, or to the population that she has studied (which maybe large or small), she is open to the charge of gerrymandering – establish-ing a domain on no other basis than that certain cases seem to fit the infer-ence under study. Donald Green and Ian Shapiro call this an “arbitrary

32 Skocpol and Somers (1980: 195). See also Goldthorpe (2003: 47) and Skocpol (1994).33 Skocpol (1979). See also Collier and Mahoney (1996: 81) and George and Bennett (2005:

120).



domain restriction.”34 The breadth of an inference must make sense; theremust be an explicable reason for including some cases and excluding oth-ers. If the inference is about oranges, then all oranges – but no apples –should be included in the population. If it is about fruit, then both applesand oranges must be included. Defining the population – as, for example,(a) oranges or (b) fruit – is thus critical to defining the inference.

The same goes for temporal boundaries. If an inference is limited toa specific period, it is incumbent upon the writer to explain why thatperiod is different from others. It will not do for writers to hide behindthe presumption that social science cannot predict the future. Theoreticalarguments cannot opt out of predicting future events if the future is likethe present in ways that are relevant to the theory. Indeed, if future evi-dence were deemed ineligible for consideration in judging the accuracy ofalready-existing theories, then writers would have effectively side-steppedany out-of-sample tests (given that, in their construction, many social sci-entific theories have already exhausted all possible evidence that is cur-rently available).

Ceteris paribus, social science gives preference to broad inferences overnarrow inferences. There are several reasons for this disciplinary prefer-ence. First, the scope of an inference usually correlates directly with itstheoretical significance. Broad empirical propositions are theory-building;narrow propositions usually have less theoretical significance (unless theyare subsumable within some larger theoretical framework). Second, broadempirical propositions usually have greater policy relevance, particularlyif they extend into the future. They help us to design effective institutionsand policies. Finally, the broader the inference, the greater its falsifiabil-ity, for the relevant evidence that might be interrogated to establish thetruth or falsehood of the inference is multiplied. For all these reasons,hypotheses should be extended as far as is logically justifiable.

Of course, no theory is infinitely extendable. Indeed, the notion of a“universal covering law” is deceptive, since even the most far-reachingsocial scientific theory has limits. The issue, then, is how to determinethe appropriate boundaries of a given proposition. An arbitrary scopecondition is one that cannot be rationally justified: there is no reason tosuppose that the theory might extend to a specified temporal or spatialboundary but no further – or nearer. A theory of revolution that per-tains to the eighteenth, nineteenth, and twentieth centuries, but not to the

34 Green and Shapiro (1999).


Preliminaries 83

twenty-first century, must justify this temporal exclusion. It must also jus-tify the decision to lump three quite diverse centuries together in one singlepopulation. Similarly, a theory of revolution that pertains to Africa butnot to Asia must justify this spatial exclusion. And a theory of revolutionthat pertains to the whole world must justify this spatial inclusion. It isnot clear that the phenomenon of revolution is similar in all cultural andgeopolitical arenas.

My point is a simple one: scope conditions may be arbitrarily large,as well as arbitrarily small. The researcher should not “define out,” or“define in,” temporal or spatial cases that do not fit the prescribed patternunless she can think of good reasons why this might be so. All populationsmust not only be specified, but also justified. Upon this justification hingesthe plausibility of the theory as well as the identification of a workableresearch design.

If, after much cogitation, the scope of an inference still seems ineradi-cably ambiguous, the writer may adopt the following expedient. Usually,it is possible to specify a limited set of cases that a given proposition mustcover if it is to make any sense at all – presumably, the set of cases that aremost similar to the case(s) under study. At the same time, it is often pos-sible to identify a larger population of cases that may be included in thecircumference of the inference, though their inclusion is more speculative –presumably because they share fewer characteristics with the case(s) understudy. If the researcher distinguishes carefully between these two popula-tions, readers will have a clear idea of the manifest scope, and the potentialscope, of a given inference.

Cross-Level Reasoning

The case study (by definition) attempts to tell us about something broaderthan the immediate subject of investigation. It is a synecdochic style ofinvestigation, studying the whole through intensive focus on one (or sev-eral) of its parts. While this inferential step from sample to population ischaracteristic of all empirical investigations (leaving aside the relativelyrare instance of investigations that are able to encompass the whole pop-ulation of interest), it is particularly problematic wherever the sample islimited to one or several, for reasons explored in the following chapter.

The wide gap between sample and population, while posing an infer-ential danger, also offers a unique opportunity. In particular, it affordsthe opportunity for a different style of causal inference, one resting ata lower level of analysis. This means that case study research is, almost



invariably, cross-level research. It operates at the level of the principalunits of analysis (the cases) as well as within selected cases (within-caseevidence). By way of conclusion to this chapter I want to emphasize theceaseless back-and-forth, cross-level nature of case study research.

Whatever the field, and whatever the tools, case studies and cross-casestudies should be viewed as partners in the iterative task of causal inves-tigation. Cross-case arguments draw on within-case assumptions, andwithin-case arguments draw on cross-case assumptions. Neither worksvery well when isolated from the other. In most circumstances, therefore,it is advisable to conduct both types of analysis. Each is made stronger bythe other.

Christopher Udry testifies to the utility of this interplay in his own areaof expertise, development economics.

The hallmark of this work is that it engages the researcher in an interactive processof detailed observation, construction of economic models, data collection, andempirical testing. An initial hypothesis is refined and clarified through detailedobservation, which informs the collection of appropriate data. As the economicenvironment is clarified during the course of fieldwork, the data-collection proce-dure can be adjusted in response. Finally, the research proceeds to formal statisticalanalysis and, one hopes, to new hypotheses. . . . The relatively small scale of theresearch facilitates this iterative process, particularly with respect to the ability ofthe researcher to quickly modify data collection.35

Ideally, the case study researcher should think carefully about cross-case evidence before conducting the time-consuming effort of an in-depthstudy focused on a single case. One should have at least a preliminary ideaof how one’s results are likely to fit into a broader set of cases. In any event,all case studies should at some point be generalized. That is, the authorshould clarify how the intensively studied case represents some broaderpopulation of cases. In many instances case study research results in a newproposition (or a significant modification of an existing proposition), onenot previously tested in a cross-case sample. If so, it is imperative thatthe case study researcher reveal, or at the very least suggest, how this newproposition might be operationalized across other cases, what the breadthof the inference is, and what a reasonable cross-case test might consist of.The exploratory case study should culminate in cross-case confirmatoryanalysis.

Granted, the case study researcher may feel that in light of the in-depthknowledge she has of her case and her comparative ignorance of other

35 Udry (2003: 107).


Preliminaries 85

cases, it would be unreasonable and irresponsible to speculate on the latter.Misgivings are understandable. However, if properly framed – as a hunchrather than a conclusion – there is no need to refrain from cross-casespeculation. These hunches are vital signposts for future research. Theybring greater clarity to the inference of primary interest and point the wayto a cumulative research agenda. No case study research should be allowedto conclude without at least a nod to how one’s case might be situatedin a broader universe of cases. Without this cross-case generalization, thecase study sits alone. Its insights, regardless of their brilliance, cannot beintegrated into a broader field of study.

The larger point, then, is that cross-case analysis is presumed in allcase study analysis. The case study is, by definition, a study of some phe-nomenon broader than the unit under investigation. The more one knowsabout this broader population of cases, the easier it will be to choosecases and to understand their significance. Similarly, the more one knowsabout individual cases, the easier it will be to interpret causal patternsthat extend across a population of cases, and to construct appropriatecausal models.36 Cross-case and within-case analysis are interdependent.It is difficult to imagine cross-case research that does not draw upon casestudy work, or case study work that disregards adjacent cases. They aredistinct, but synergistic, tools in the analysis of social life.37

36 Gordon and Smith (2004).37 The same point was made many decades ago by L. L. Bernard (1928: 310), and again by

Samuel Stouffer (1941: 357).


5

Techniques for Choosing Cases

Case study analysis focuses on a small number of cases that are expectedto provide insight into a causal relationship across a larger populationof cases. This presents the researcher with a formidable problem of caseselection. Which cases should be chosen?

In large-sample research, case selection is usually handled by someversion of randomization. If a sample consists of a large enough num-ber of independent random draws, the selected cases are likely to befairly representative of the overall population on any given variable.Furthermore, if cases in the population are distributed homogeneouslyacross the ranges of the key variables, then it is probable that somecases will be included from each important segment of those ranges,thus providing sufficient leverage for causal analysis. (For situations inwhich cases with theoretically relevant values of the variables are rare, astratified sample that oversamples some subset of the population may beemployed.)

A demonstration of the fact that random sampling is likely to producea representative sample is shown in Figure 5.1, a histogram of the meanvalues of 500 random samples, each consisting of 1,000 cases. For eachcase, one variable has been measured: a continuous variable that fallssomewhere between zero and one. In the population, the mean value ofthis variable is 0.5. How representative are the random samples? Onegood way of judging this is to compare the means of each of the 500random samples to the population mean. As can be seen in the figure, allof the sample means are very close to the population mean. So randomsampling was a success, and each of the 500 samples turns out to be fairlyrepresentative of the population.

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However, in case study research the sample is small (by definition),and this makes randomization problematic. Consider what would hap-pen if the sample size were changed from 1,000 cases to only 5 cases.The results are shown in Figure 5.2. On average, these small-N ran-dom samples produce the right answer, so the procedure culminates inresults that are unbiased. However, many of the sample means are ratherfar from the population mean, and some are quite far indeed. Hence,even though this case-selection technique produces representative sam-ples on average, any given sample may be wildly unrepresentative. Instatistical terms, the problem is that small sample sizes tend to pro-duce estimates with a great deal of variance – sometimes referred toas a problem of precision. For this reason, random sampling is unre-liable in small-N research. (Note that in this chapter “N” refers tocases, not observations.) Moreover, there is no guarantee that a fewcases, chosen randomly, will provide leverage into the research questionthat animates an investigation. The sample might be representative, butuninformative.

If random sampling is inappropriate as a selection method in casestudy research, how, then, is one to choose a sample comprised ofone or several cases? Keep in mind that the goals of case selection



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figure 5.2. Sample means of small-sample draws. A histogram showing the meanvalues of one variable in 500 samples of 5 cases each. Population mean = 0.5.

remain the same regardless of the size of the chosen sample. Large-Ncross-case analysis and case study analysis both aim to identify cases thatreproduce the relevant causal features of a larger universe (representative-ness) and provide variation along the dimensions of theoretical interest(causal leverage). In case study research, however, these goals must bemet through purposive (nonrandom) selection procedures. These may beenumerated according to nine techniques, from which we derive nine casestudy types: typical, diverse, extreme, deviant, influential, crucial, path-way, most-similar, and most-different.

Table 5.1 summarizes each type, including its general definition, a tech-nique for identifying it within a population of potential cases, its uses,and its probable representativeness. While each of these techniques isnormally practiced on one or several cases (the diverse, most-similar, andmost-different methods require at least two), all may employ additionalcases – with the proviso that, at some point, they will no longer offer anopportunity for in-depth analysis and will thus no longer be case studiesin the usual sense.

The main point of this chapter is to show how case-selection proceduresrest, at least implicitly, upon an analysis of a larger population of potentialcases. The case(s) identified for intensive study is chosen from a popula-tion, and the reasons for this choice hinge upon the way in which it is



table 5.1. Techniques of case-selection

1. Typical� Definition: Cases (one or more) are typical examples of some cross-caserelationship.

� Cross-case technique: A low-residual case (on-lier).� Uses: Hypothesis testing.� Representativeness: By definition, the typical case is representative.2. Diverse� Definition: Cases (two or more) illuminate the full range of variation on X1, Y,or X1/Y.

� Cross-case technique: Diversity may be calculated by (a) categorical values ofX1 or Y (e.g., Jewish, Catholic, Protestant), (b) standard deviations of X1 or Y(if continuous), or (c) combinations of values (e.g., based on cross-tabulations,factor analysis, or discriminant analysis).

� Uses: Hypothesis generating or hypothesis testing.� Representativeness: Diverse cases are likely to be representative in the minimalsense of representing the full variation of the population (though they mightnot mirror the distribution of that variation in the population).

3. Extreme� Definition: Cases (one or more) exemplify extreme or unusual values on X1 orY relative to some univariate distribution.

� Cross-case technique: A case lying many standard deviations away from themean of X1 or Y.

� Uses: Hypothesis generating (open-ended probe of X1 or Y).� Representativeness: Achievable only in comparison to a larger sample of cases.

4. Deviant� Definition: Cases (one or more) deviate from some cross-case relationship.� Cross-case technique: A high-residual case (outlier).� Uses: Hypothesis generating (to develop new explanations of Y).� Representativeness: After the case study is conducted, it may be corroboratedby a cross-case test, which includes a general hypothesis (a new variable) basedon the case study research. If the case is now an on-lier, it may be consideredrepresentative of the new relationship.

5. Influential� Definition: Cases (one or more) with influential configurations of theindependent variables.

� Cross-case technique: Hat matrix or Cook’s distance.� Uses: Hypothesis testing (to verify the status of cases that may influence theresults of a cross-case analysis).

� Representativeness: Not pertinent, given the goals of the influential-case study.

6. Crucial� Definition: Cases (one or more) are most- or least-likely to exhibit a givenoutcome.

� Cross-case technique: Qualitative assessment of relative crucialness.

(continued)



table 5.1 (continued)

� Uses: Hypothesis testing (confirmatory or disconfirmatory).� Representativeness: Assessable by reference to prior expectations about thecase and the population.

7. Pathway� Definition: Cases (one or more) where X1, and not X2, is likely to have causeda positive outcome (Y=1).

� Cross-case technique: Cross-tab (for categorical variables) or residual analysis(for continuous variables).

� Uses: Hypothesis testing (to probe causal mechanisms).� Representativeness: May be tested by examining residuals for the chosen cases.

8. Most-similar� Definition: Cases (two or more) are similar on specified variables other thanX1 and/or Y.

� Cross-case technique: Matching.� Uses: Hypothesis generating or hypothesis testing.� Representativeness: May be tested by examining residuals for the chosen cases.

9. Most-different� Definition: Cases (two or more) are different on specified variables other thanX1 and Y.

� Cross-case technique: The inverse of the most-similar method of large-N caseselection (see above).

� Uses: Hypothesis generating or hypothesis testing (eliminating deterministiccauses).

� Representativeness: May be tested by examining residuals for the chosen cases.

situated within that population. This is the origin of the terminology justlisted – typical, diverse, extreme, and so on. It follows that case-selectionprocedures in case study research may build upon prior cross-case analysisand depend, at the very least, upon certain assumptions about a broaderpopulation. This, in turn, reinforces a central perspective of the book:case study analysis does not exist, and is impossible to conceptualize, inisolation from cross-case analysis.

To be sure, the sort of cross-case analysis that might be possible in agiven research context rests on how large the population of potential casesis, on how much information one has about these cases, on what sort ofgeneral model might be constructed, and with what degree of confidencethat model might be applied. In order for most quantitative (statistical)case-selection techniques to be fruitful, several caveats must be satisfied.First, the inference must pertain to more than several cases; otherwise,



statistical analysis is usually problematic. Second, relevant data must beavailable for that population, or a significant sample of that population,on key variables, and the researcher must feel reasonably confident inthe accuracy and conceptual validity of these variables. Third, all thestandard considerations of statistical research (e.g., identification, specifi-cation, robustness) must be carefully considered and, wherever possible,investigated. I shall not dilate further on these familiar issues except towarn the researcher against the unthinking use of statistical techniques.1

When these requirements are not met, the researcher must employ aqualitative approach to case selection. Thus, the point of this chapter isnot to insist upon quantitative techniques of case selection in case studyresearch. My purpose, rather, is to elucidate general principles that mightguide the process of case selection in case study research, whether the tech-nique is quantitative or qualitative. Some of these principles are alreadywidely known and widely practiced. Others are less common, or lesswell understood. Most of these methods are viable – indeed, are virtuallyidentical – in qualitative and quantitative contexts. Hence, the statisticalsections of this chapter usually simply reformulate the logic of qualitativecase-selection procedures as they might be applied to large populationswhere the foregoing caveats apply.

Typical Case

In order for a focused case study to provide insight into a broader phe-nomenon, it must be representative of a broader set of cases. It is in thiscontext that one may speak of a typical-case approach to case selection.The typical case exemplifies what is considered to be a typical set of values,given some general understanding of a phenomenon. By construction, thetypical case is also a representative case; I employ these two terms syn-onymously.2 (The antonym, deviance, is discussed in a later section.)

Some typical cases serve an exploratory role. Here, the author choosesa case based upon a set of descriptive characteristics and then probes forcausal relationships. Robert and Helen Lynd selected a single city “to be

1 Gujarati (2003); Kennedy (2003). Interestingly, the potential of cross-case statistics inhelping to choose cases for in-depth analysis is recognized in some of the earliest discus-sions of the case study method (e.g., Queen 1928: 226).

2 The latter term is often employed in the psychological literature (e.g., Hersen and Barlow1976: 24).



as representative as possible of contemporary American life.” Specifically,they were looking for a city with

1) a temperate climate; 2) a sufficiently rapid rate of growth to ensure the presenceof a plentiful assortment of the growing pains accompanying contemporary socialchange; 3) an industrial culture with modern, high-speed machine production;4) the absence of dominance of the city’s industry by a single plant (i.e., not aone-industry town); 5) a substantial local artistic life to balance its industrialactivity . . . ; and 6) the absence of any outstanding peculiarities or acute localproblems which would mark the city off from the midchannel sort of Americancommunity.3

After examining a number of options, the Lynds decided that Muncie,Indiana, was more representative than, or at least as representative as,other midsized cities in America, thus qualifying as a typical case.

This is an inductive approach to case selection. Note that typicalitymay be understood according to the mean, median, or mode on a par-ticular dimension; there may be multiple dimensions (as in the foregoingexample); and each may be differently weighted (some dimensions may bemore important than others). Where the selection criteria are multidimen-sional and a large sample of potential cases is in play, some form of factoranalysis may be useful in identifying the most-typical case(s). Althoughthe Lynds did not employ a statistical model to evaluate potential cases,it is easy to see how they might have done so, at least along the first fivecriteria. (The final criteria would be difficult to operationalize in a largesample, since it involves “peculiarities” of any sort.)

However, the more common employment of the typical-case methodinvolves a causal model of some phenomenon of theoretical interest. Here,the researcher has identified a particular outcome (Y), and perhaps aspecific X1/Y hypothesis, which she wishes to investigate. In order to doso, she looks for a typical example of that causal relationship. Intuitively,one imagines that a case selected according to the mean values of allparameters must be a typical case relative to some causal relationship.However, this is by no means assured.

Suppose that the Lynds were primarily interested in explaining feelingsof trust/distrust among members of different social classes (one of theimplicit research goals of the Middletown study). This outcome is likelyto be affected by many factors, only some of which are included in theirsix selection criteria. So choosing cases with respect to a causal hypothesis

3 Lynd and Lynd (1929/1956), quoted in Yin (2004: 29–30).



involves, first of all, identifying the relevant variables. It involves, secondly,the selection of a case that has “typical” values relative to the overallcausal model; it is well explained.

Note that cases with atypical scores on a particular dimension (e.g.,very high or very low) may still be typical examples of a causal relation-ship. Indeed, they may be more typical than cases whose values lie closeto the mean.

Note also that because the typical case embodies a typical value onsome set of variables, the variance of interest to the researcher must liewithin that case. Specifically, the typical case of some phenomenon maybe helpful in exploring causal mechanisms and in solving identificationproblems (e.g., endogeneity between X1 and Y, an omitted variable thatmay account for X1 and Y, or some other spurious causal association).Depending upon the results of the case study, the author may confirman existing hypothesis, disconfirm that hypothesis, or reframe it in a waythat is consistent with the findings of the case study.

Cross-Case TechniqueHow might one identify a typical case from a large population of poten-tial cases? If the causal relationship involves only a single independentvariable and if the relationship is quite strong, it may be possible toidentify typical cases simply by eyeballing the evidence. A strong posi-tive association between X1 and Y means that a case with similar (high,low, or middling) values on X1 and Y is probably a typical case. How-ever, there are few bivariate causal relationships in social science. Usually,more than one causal factor must be evaluated, even if the additional vari-ables serve only as controls. Moreover, without some overall assessmentof the cross-case evidence it may be difficult to say whether the generalrelationship is positive or negative, strong or weak. Thus, in any large-Nsample (i.e., whenever the number of potential cases is great) it is advis-able to perform a formal cross-case analysis in order to identify “typical”cases.

Suppose that an arbitrary case in the population, denoted as case i,has a known score on each of several relevant variables. For the sakeof economy of language, let the variables involved in the relationship belabeled yi and x1,i, . . . xK,i, where yi is the score of case i on one variable andeach of the xK,i’s is the score of case i on one of the K other variables underconsideration. Thus, the relationship involves a total of K + 1 variables.K can be any integer greater than or equal to 1.



With these symbols, the established relationships among the variablescan be expressed mathematically. The idea is to find a function, f(), suchthat the average score of y for cases with some specific set of scores onx1 . . . xK is equal to f(x1, . . . xK). Thus, the function f() should be chosento capture the key ideas about the relationship of interest. A familiarexample may make this discussion clearer.

Often, researchers choose an additive (linear) function to play the roleof f(). Using traditional statistical notation, in which the average score ofyi across infinite repetitions of case i is denoted by its expectation, E(yi),a linear function represents a relationship in which:

E(yi ) = β0 + β1x1,i + · · · + βKxK,i (5.1)

Each of the βK’s in this equation represents an unknown constant. Regres-sion analysis allows researchers to use known information about the y andx1 . . . xK variables for a set of cases to estimate these unknown constants.Estimates of βK will be denoted here as bK.

Using this terminology, we can now develop a formula for the degree towhich a particular case is typical in light of a given relationship. A case is“typical” in the terms of small-N methodology to the extent that its scoreon the y variable is close to the average score on that variable for a casewith the same scores on the x1 . . . xK variables, as given by equation 5.1.That is,

Typicality(i) = −abs[yi − E(yi |x1,i , . . . xK,i )] (5.2)

= −abs[yi − b0 + b1x1,i + · · · + bKxK,i ]

According to this discussion, the typicality of a case with respect to aparticular relationship is simply −1 times the absolute value of that case’serror term (its residual) in regression analysis. This measure of typicalityranges, in theory, from negative infinity to zero. When a case falls close tothe regression line, its typicality will be just below zero. When a case fallsfar from the regression line, its typicality will be far below zero. Typicalcases have small residuals.

In a large-N sample, there will often be many cases with high (i.e., near-zero) typicality scores. In such situations, researchers may elect not tofocus on the cases with the highest estimated typicality, for such estimatesmay not be accurate enough to distinguish among several almost-identicalcases. Instead, researchers may choose to randomly select from the setof cases with very high typicality, or to choose from among these casesaccording to additional criteria, such as those to be discussed here, or by



reason of practicality (cost, convenience, etc.). However, scholars shouldtry to avoid selecting from among the set of typical cases in a way thatis correlated with relevant omitted variables; such selection procedurescomplicate the task of causal inference.

Consider the (presumably causal) relationship between economicdevelopment and level of democracy.4 Democracy is understood here asa continuous concept along a twenty-one-point scale, from −10 (mostautocratic) to +10 (most democratic).5 Economic development is mea-sured in standard fashion by per capita GDP.6 Figure 5.3 displays thisrelationship in the form of a bivariate scatterplot. The classical result isstrikingly illustrated: wealthy countries are almost exclusively democratic.(For heuristic purposes, certain simplifying assumptions are adopted. Ishall assume, for example, that this measure of democracy is continuousand unbounded.7 I shall assume, more importantly, that the true relation-ship between economic development and democracy is log-linear, positive,and causally asymmetric, with economic development treated as exoge-nous and democracy as endogenous.8)

Given this general relationship, how might a set of “typical” cases beselected? Recall that the Y variable is simply the democracy score, andthere is only one independent variable: logged per capita GDP. Hence,the simplest relevant model is:

E(Polityi ) = β0 + β1GDPi (5.3)

For our purposes, the most important feature of this model is the resid-uals for each case. Figure 5.4 shows a histogram of these residuals. Obvi-ously, a fairly large number of cases have quite low residuals and thereforemight be considered typical. A higher proportion of cases fall far belowthe regression line than far above it, suggesting that the model may be

4 Lipset (1959). Whether economic development has only the effect of maintaining demo-cratic regimes (Przeworski et al. 2000) or also of causing regime transitions (Boix andStokes 2003) is not relevant to the present discussion, where I assume a simple linearrelationship between wealth and democracy.

5 This scoring derives from the Polity2 variable in the Polity IV dataset (Marshall andJaggers 2005).

6 Data are drawn from the Penn World Tables dataset (Summers and Heston 1991).7 But see Treier and Jackman (2003).8 But see Gerring et al. (2005) and Przeworski et al. (2000).



Logged 1995 per capita GDP

1995

com

bine

d po

lity

scor

e

-50

510

7 8 9 10

figure 5.3. The presumed relationship between economic development anddemocracy. A scatterplot showing level of democracy (on the vertical axis)and level of wealth (on the horizontal axis) of all available countries in 1995.N = 131.

incomplete. Hopefully, within-case analysis will be able to shed light onthe reasons for the asymmetry.9

Because of the large number of cases with quite small residuals, theresearcher will have a range of options for selecting typical cases. Indeed,in this example, twenty-six cases have a typicality score between 0 and −1.Any or all of these might reasonably be selected as typical cases withrespect to the model described in equation 5.3.

ConclusionTypicality responds to the first desideratum of case selection, that thechosen case be representative of a population of cases (as defined bythe primary inference). Even so, it is important to remind ourselves thata single-minded pursuit of representativeness does not ensure that thisdesideratum will be achieved. Indeed, the issue of case representativenessis not an issue that can ever be definitively settled in a case study for-mat. When one refers to a “typical case” one is saying, in effect, that theprobability of a case’s representativeness is high, relative to other cases.

Note that the measure of typicality introduced here, the size of a case’sresidual, can be misleading if the statistical model is misspecified. And

9 In this example, the asymmetry is probably due to the failure of the model to take intoaccount the restricted range of the dependent variable, as discussed earlier.



Residual from robust regression

Num

ber

of c

ases

-20 -15 -10 10-5 0 5

1015

2025

300

5

figure 5.4. Potential typical cases. A histogram of the residuals from a robustregression of logged per capita GDP on level of democracy.

it provides little insurance against errors that are purely stochastic. Acase may lie directly on the regression line but still be, in some impor-tant respect, atypical. For example, it might have an odd combination ofvalues; the interaction of variables might be different from that in othercases; or unusual causal mechanisms might be at work. Most important,an analysis of residuals does not address problems of sample bias. If thelarge-N sample is not representative of the relevent population then anyanalysis based on the former is apt to be flawed. Typicality does not ensurerepresentativeness. For these reasons, it is important to supplement a sta-tistical analysis of cases with evidence drawn from the case in question(the case study itself) and with our general knowledge of the world. Oneshould never judge a case solely by its residual. Yet, all other things beingequal, a case with a low residual is less likely to be unusual than a case witha high residual, and to this extent the method of case selection outlinedhere may be a helpful guide to case study researchers faced with a largenumber of potential cases.

Diverse Case

A second case-selection strategy has as its primary objective the achieve-ment of maximum variance along relevant dimensions. I refer to this as a



diverse-case method. For obvious reasons, this method requires the selec-tion of a set of cases – at minimum, two – that are intended to representthe full range of values characterizing X1, Y, or some particular X1/Yrelationship.10

Where the individual variable of interest is categorical (on/off, red/black/blue, Jewish/Protestant/Catholic), the identification of diversity isreadily apparent. The investigator simply chooses one case from eachcategory. For a continuous variable, the choices are not so obvious. How-ever, the researcher is well advised to choose both extreme values (highand low), and perhaps the mean or median as well. One may also lookfor break-points in the distribution that seem to correspond to categoricaldifferences among cases. Or one may follow a theoretical hunch aboutwhich threshold values count – that is, which ones are likely to producedifferent values on Y.

Another sort of diverse case takes account of the values of multiplevariables (i.e., a vector) rather than a single variable. If these variablesare categorical, the identification of causal types rests upon the inter-section of each category. Two dichotomous variables produce a matrixwith four cells; three dichotomous variables produce a matrix of eightcells, and so forth. If all variables are deemed relevant to the analysis,the selection of diverse cases mandates the selection of one case drawnfrom within each cell. Let us say that an outcome is thought to beaffected by sex, race (black/white), and marital status. Here, a diverse-case strategy of case selection would identify one case within each of theseintersecting cells – a total of eight cases. Again, things become more com-plicated when one or more of the factors is continuous, rather than cat-egorical. Here, the diversity of case values do not fall neatly into cells.Rather, these cells must be created by fiat – for example, high, medium,low.

It will be seen that where multiple variables are under consideration,the logic of diverse-case analysis rests upon the logic of typological the-orizing – where different combinations of variables are assumed to haveeffects on an outcome that vary across types. George and Bennett definea typological theory as

10 This method has not been given much attention by qualitative methodologists; hence, theabsence of a generally recognized name. It bears some resemblance to J. S. Mill’s JointMethod of Agreement and Difference (Mill 1843/1872), which is to say, a mixture ofmost-similar and most-different analysis, as discussed later. Patton (2002: 234) employsthe concept of “maximum variation (heterogeneity) sampling.”



a theory that specifies independent variables, delineates them into nominal, ordi-nal, or interval categories, and provides not only hypotheses on how these vari-ables operate singly, but contingent generalizations on how and under what con-ditions they behave in specified conjunctions or configurations to produce effectson specified dependent variables. We call specified conjunctions or configurationsof the variables “types.” A fully specified typological theory provides hypotheseson all of the mathematically possible types relating to a phenomenon, or on thefull ‘property space,’ to use Lazarsfeld’s term. Typological theories are rarely fullyspecified, however, because researchers are usually interested only in the types thatare relatively common or that have the greatest implications for theory-buildingor policy-making.11

George and Smoke, for example, wish to explore different types of deter-rence failure – by “fait accompli,” by “limited probe,” and by “controlledpressure.” Consequently, they wish to find cases that exemplify each typeof causal mechanism.12

Diversity may thus refer to a range of variation on X1 or Y, or to aparticular combination of causal factors (with or without a considerationof the outcome). In each instance, the goal of case selection is to capturethe full range of variation along the dimension(s) of interest.

Cross-Case TechniqueSince diversity can mean many things, its employment in a large-N settingis necessarily dependent upon how it is understood. If it is understood topertain only to a single variable (X1 or Y), then the task is fairly simple,as we have discussed. Univariate traits are usually easy to discover in alarge-N setting through descriptive statistics or through visual inspectionof the data.

Where diversity refers to particular combinations of variables, the rele-vant cross-case technique is some version of stratified random sampling (ina probabilistic setting)13 or Qualitative Comparative Analysis (in a deter-ministic setting).14 If the researcher suspects that a causal relationship isaffected not only by combinations of factors but also by their sequencing,

11 George and Bennett (2005: 235). See also Elman (2005) and Lazarsfeld and Barton(1951).

12 More precisely, George and Smoke (1974: 534, 522–36, Chapter 18; see also discussionin Collier and Mahoney 1996: 78) set out to investigate causal pathways and discovered,in the course of their investigation of many cases, these three causal types. But for ourpurposes what is important is that the final sample include at least one representative ofeach “type.”

13 See Cochran (1977).14 Ragin (2000).



then the technique of analysis must incorporate temporal elements.15

Thus, the method of identifying causal types rests upon whatever methodof identifying causal relationships is presumed to exist.

Note that the identification of distinct case types is intended to identifygroups of cases that are internally homogeneous (in all respects that mightaffect the causal relationship of interest). Thus, the choice of cases withineach group should not be problematic, and may be accomplished throughrandom sampling. However, if there is suspected diversity within eachcategory, then measures should be taken to assure that the chosen casesare typical of each category. A case study should not focus on an atypicalmember of a subgroup.

Indeed, considerations of diversity and typicality often go together.Thus, in a study of globalization and social welfare systems, Duane Swankfirst identifies three distinctive groups of welfare states: “universalistic”(social democratic), “corporatist conservative,” and “liberal.” Next, helooks within each group to find the most-typical cases. He decides thatthe Nordic countries are more typical of the universalistic model thanthe Netherlands, since the latter has “some characteristics of the occu-pationally based program structure and a political context of ChristianDemocratic-led governments typical of the corporatist conservativenations.”16 Thus, the Nordic countries are chosen as representative caseswithin the universalistic case type, and are accompanied in the case-studyportion of his analysis by other cases chosen to represent the other welfarestate types (corporatist conservative and liberal).

ConclusionEncompassing a full range of variation is likely to enhance the representa-tiveness of the sample of cases chosen by the researcher. This is a distinctadvantage. Of course, the inclusion of a full range of variation may dis-tort the actual distribution of cases across this spectrum. If there are more“high” cases than “low” cases in a population and the researcher choosesonly one high case and one low case, the resulting sample of two is not per-fectly representative. Even so, the diverse-case method often has strongerclaims to representativeness than any other small-N sample (including thetypical case). The selection of diverse cases has the additional advantageof introducing variation on the key variables of interest. A set of diverse

15 Abbott (2001); Abbott and Forrest (1986); Abbott and Tsay (2000).16 Swank (2002: 11). See also Esping-Andersen (1990).



cases is, by definition, a set of cases that encompasses a range of high andlow values on relevant dimensions.

There is, therefore, much to recommend this method of case selection. Isuspect that these advantages are commonly understood and are appliedon an intuitive level by case study researchers. However, the lack of arecognizable name – and an explicit methodological defense – has made itdifficult for case study researchers to identify this method of case selection,and to explain its logic to readers.

Extreme Case

The extreme-case method selects a case because of its extreme value on anindependent or dependent variable of interest.17 Thus, studies of domesticviolence may choose to focus on extreme instances of abuse.18 Studies ofaltruism may focus on those rare individuals who risk their lives to helpothers (e.g., Holocaust resisters).19 Studies of ethnic politics may focuson the most heterogeneous societies (e.g., Papua New Guinea) in order tobetter understand the role of ethnicity in a democratic setting.20 Studiesof industrial policy often focus on the most successful countries (e.g., theNICs),21 and so forth.22

Often an extreme case corresponds to a case that is considered tobe prototypical or paradigmatic of some phenomena of interest. This isbecause concepts are often defined by their extremes, that is, their idealtypes. German fascism defines the concept of fascism in part becauseit offers the most extreme example of that phenomenon. However, themethodological value of this case, and others like it, derives from itsextremity (along some dimension of interest), not from its theoreticalstatus or its status in the literature on a subject.

The notion of “extreme” may now be defined more precisely. Anextreme value is an observation that lies far away from the mean of a given

17 It does not make sense to apply the extreme-case method in a confirmatory/disconfirmatory analysis. If a particular causal relationship is at issue, then both X1and Y must be taken into account when choosing cases, as described in the various sce-narios that follow. At present, therefore, we shall assume that the researcher has a generalquestion in mind, but not a specific hypothesis.

18 Browne (1987).19 Monroe (1996).20 Reilly (2000/2001).21 Deyo (1987).22 For further examples, see Collier and Mahoney (1996); Geddes (1990); and Tendler

(1997).



distribution. For a continuous variable, the distance from the mean maybe in either direction (positive or negative). For a dichotomous variable(present/absent), I understand extreme to mean unusual. If most casesare positive along a given dimension, then a negative case constitutes anextreme case. If most cases are negative, then a positive case constitutesan extreme case. All things being equal, one is concerned not only withcases where something “happened,” but also with cases where somethingdid not. It is the rareness of the value that makes a case valuable, inthis context, not its positive or negative value.23 Thus, if one is studyingstate capacity, a case of state failure is probably more informative thana case of state endurance simply because the former is more unusual.Similarly, if one is interested in incest taboos, a culture where the incesttaboo is absent or weak is probably more useful than a culture where it ispresent. Fascism is more important than nonfascism; and so forth. Thereis a good reason, therefore, why case studies of revolution tend to focuson “revolutionary” cases. Theda Skocpol had much more to learn fromFrance than from Austro-Hungary, since France was more unusual thanAustro-Hungary within the population of nation-states that Skocpolwas concerned to explain.24 The reason is quite simple: there are fewerrevolutionary cases than nonrevolutionary cases; thus, the variationthat one wishes to explore as a clue to causal relationships is encap-sulated in these cases, viewed against a backdrop of nonrevolutionarycases.

Cross-Case TechniqueAs stated, extreme cases lie far from the mean of a variable. Extremity(E), for the ith case, can be defined in terms of the sample mean (X) andthe standard deviation (s) for that variable:

Ei =∣∣∣∣Xi − X

s

∣∣∣∣ (5.4)

This definition of extremity is the absolute value of the standardized(“Z”) score for the ith case. Cases with a large Ei qualify as extreme.Sometimes, the only criterion is a relative one. The researcher wishes tofind the most extreme case(s) available. At other times, it may be helpful

23 Traditionally, methodologists have conceptualized cases as having “positive” or “nega-tive” values (e.g., Emigh 1997; Mahoney and Goertz 2004; Ragin 2000: 60; Ragin 2004:126).

24 Skocpol (1979).


Techniques for Choosing Cases 103N

umbe

r of

cas

es

010

2030

40

Extremeness

0.0 0.5 1.0 1.5 2.0

figure 5.5. Potential extreme cases. A histogram of the “extremeness” of all coun-tries on the dimension of democracy, as measured by standard deviations fromthe mean (absolute value).

to set an arbitrary threshold. Under assumptions of normality, cases withan extremeness score smaller than two would generally not be consideredextreme. If the researcher wishes to be more conservative in classifyingcases as extreme, a higher threshold may be employed. In general, thechoice of threshold is left to the researcher, to be made in a way that isappropriate to the research problem at hand.

The mean of our democracy variable is 2.76, suggesting that the coun-tries in the 1995 dataset tend to be somewhat more democratic thanauthoritarian (zero is defined as the break-point between democracy andautocracy). The standard deviation is 6.92, implying that there is a fairamount of scatter around the mean.

Figure 5.5 shows a histogram of the extremeness scores for all countrieson level of democracy. As can easily be seen, no cases have extremenessscores greater than two. The two countries with the highest scores areQatar and Saudi Arabia. These countries, which both have a democracyscore of −10 for 1995, are probably the two best candidates for extreme-case analysis.



ConclusionThe extreme-case method appears to violate the social science folk wisdomwarning us not to “select on the dependent variable.”25 Selecting caseson the dependent variable is indeed problematic if a number of cases arechosen, all of which lie on one end of a variable’s spectrum (they are allpositive or negative), and if the researcher then subjects this sample tocross-case analysis as if it were representative of a population.26 Resultsfor this sort of analysis would almost assuredly be biased. Moreover, therewill be little variation to explain, since the values of each case are explicitlyconstrained.

However, this is not the proper employment of the extreme-casemethod. (It is more appropriately labeled an extreme-sample method.)The extreme-case method refers back to a larger sample of cases that liein the background of the analysis and provide a full range of variationas well as a more representative picture of the population. It is a self-conscious attempt to maximize variance on the dimension of interest, notto minimize it. If this population of cases is well understood – through theauthor’s own cross-case analysis, through the work of others, or throughcommon sense – then a researcher may justify the selection of a singlecase exemplifying an extreme value for within-case analysis. If not, theresearcher may be well advised to follow a diverse-case method (see theearlier discussion).

By way of conclusion, let us return to the problem of representativeness.In the context of causal analysis, representativeness refers to a case thatexemplifies values on X1 and Y that conform to a general pattern. In across-case model, the representativeness of an individual case is gaugedby the size of its residual. The representative case is therefore a typicalcase (as already discussed), not a deviant case (as will be discussed). Itwill be seen that an extreme case may be typical or deviant. There issimply no way to tell, because the researcher has not yet specified a causalproposition. Once such a causal proposition has been specified, we maythen ask whether the case in question is similar to some population ofcases (in all respects that might affect the X1/Y relationship of interest).It is at this point that it becomes possible to say, within the context of across-case statistical model, whether a case lies near to, or far from, the

25 Geddes (1990); King, Keohane, and Verba (1994). See also discussions in Brady andCollier (2004); Collier and Mahoney (1996); and Rogowski (1995).

26 The exception would be a circumstance in which the researcher intends to disprove adeterministic argument (Dion 1998).



regression line. However, this sort of analysis means that the researcheris no longer pursuing an extreme-case method. The extreme-case methodis purely exploratory – a way of probing possible causes of Y, or possibleeffects of X1, in an open-ended fashion. If the researcher has some notionof what additional factors might affect the outcome of interest, or ofwhat relationship the causal factor of interest has to Y, then she ought topursue one of the other methods explored elsewhere in this chapter. Thisalso implies that an extreme-case method may transform into a differentkind of approach as a study evolves, that is, as a more specific hypothesiscomes to light. Useful “extreme” cases at the outset of a study may proveless useful at a later stage of analysis.

Deviant Case

The deviant-case method selects the case(s) that, by reference to some gen-eral understanding of a topic (either a specific theory or common sense),demonstrates a surprising value. Barbara Geddes notes the importance ofdeviant cases in medical science, where researchers are habitually focusedon that which is pathological (according to standard theory and practice).The New England Journal of Medicine, one of the premier journals of thefield, carries a regular feature entitled “Case Records of the MassachusettsGeneral Hospital.” These articles bear titles like the following: “An 80-Year-Old Woman with Sudden Unilateral Blindness” or “A 76-Year-OldMan with Fever, Dyspnea, Pulmonary Infiltrates, Pleural Effusions, andConfusion.”27 Similarly, medical researchers are keen to investigate thoserare individuals who have not succumbed, despite repeated exposure, tothe AIDS virus.28 Why are they resistant? What is different about thesepeople? What can we learn about AIDS in other patients by observingpeople who have built-in resistance to this disease?

Case studies in psychology and sociology are often comprised of devi-ant (in the social sense) persons or groups. In economics, case studiesmay consist of countries or businesses that overperform (e.g., Botswana,Microsoft) or underperform (e.g., Britain through most of the twentiethcentury; Sears in recent decades) relative to some set of expectations. In

27 Geddes (2003: 131). For other examples of case work from the annals of medicine, see“Clinical Reports” in The Lancet; “Case Studies” in The Canadian Medical AssociationJournal; and various issues of the Journal of Obstetrics and Gynecology, often devotedto clinical cases (discussed in Jenicek 2001: 7). For examples from the subfield of com-parative politics, see Kazancigil (1994).

28 Buchbinder and Vittinghoff (1999); Haynes, Pantaleo, and Fauci (1996).



political science, case studies may focus on countries where the welfarestate is more developed (e.g., Sweden) or less developed (e.g., the UnitedStates) than one would expect, given a set of general expectations aboutwelfare state development.

In all fields, the deviant case is closely linked to the investigation of the-oretical anomalies. Indeed, to say “deviant” is to imply “anomalous.”29

Note that while extreme cases are judged relative to the mean of a singledistribution (the distribution of values along a single dimension), deviantcases are judged relative to some general model of causal relations. Thedeviant-case method selects cases that, by reference to some general cross-case relationship, demonstrate a surprising value. They are “deviant” inthat they are poorly explained by the multivariate model. The impor-tant point is that deviantness can only be assessed relative to the general(quantitative or qualitative) model employed.

This means that the relative deviantness of a case is likely to changewhenever the general model is altered. For example, the United States isa deviant welfare state when this outcome is gauged relative to societalwealth. But it is less deviant – and perhaps not deviant at all – whencertain additional (political and societal) factors are included in the model,as discussed in the epilogue. Deviance is model-dependent. Thus, whendiscussing the concept of the deviant case, it is helpful to ask the followingquestion: relative to what general model (or set of background factors) isCase A deviant?

The purpose of a deviant-case analysis is usually to probe for new – butas yet unspecified – explanations. (If the purpose is to disprove an extanttheory, I shall refer to the study as a crucial case, as will be discussed later.)Thus, the deviant-case method is only slightly more determinate than theextreme-case method. It, too, is an exploratory form of research. Theresearcher hopes that causal processes within the deviant case will illus-trate some causal factor that is applicable to other (deviant) cases. Thismeans that a deviant-case study usually culminates in a general proposi-tion – one that may be applied to other cases in the population.

Cross-Case TechniqueIn statistical terms, deviant-case selection is the opposite of typical-caseselection. Where a typical case lies as close as possible to the prediction

29 For a discussion of the important role of anomalies in the development of scientifictheorizing, see Elman (2003) and Lakatos (1978). For examples of deviant-case researchdesigns in the social sciences, see Amenta (1991); Coppedge (2004); Eckstein (1975);Emigh (1997); and Kendall and Wolf (1949/1955).



of a formal, mathematical representation of the hypothesis at hand, adeviant case lies as far as possible from that prediction. Referring back tothe model developed in equation 5.3, we can define the extent to which acase deviates from the predicted relationship as follows:

Deviance(i) = abs[yi − E(yi |x1,i, . . . xK,i )] (5.5)

= abs[yi − b0 + b1x1,i + · · · + bKxK,i ]

Deviance ranges from 0, for cases exactly on the regression line, toa theoretical limit of infinity. Researchers will usually be interested inselecting from the cases with the highest overall estimated deviance.

In our running example, a two-variable model with economic devel-opment (X1) and democracy (Y), the most deviant cases fall below theregression line. This can be seen in Figure 5.4. In fact, all eight cases witha deviance score of more than ten have negative residuals; their scores onthe outcome are lower than they “should” be, given their level of devel-opment. These eight cases are Croatia, Cuba, Indonesia, Iran, Morocco,Singapore, Syria, and Uzbekistan. Our general model of democracy doesnot explain these cases very well. Quite possibly, we could develop a bet-ter model if we understood what – aside from GDP per capita – mightbe driving the choice of regime type in these polities. This is the usualpurpose for which deviant-case analysis is employed.

ConclusionAs I have noted, the deviant-case method is an exploratory form of anal-ysis. As soon as a researcher’s exploration of a particular case has iden-tified a factor to explain that case, it is no longer (by definition) deviant.(The exception would be a circumstance in which a case’s outcome isdeemed to be accidental or idiosyncratic, and therefore inexplicable byany general model.) If the new explanation can be accurately measured asa single variable (or set of variables) across a larger sample of cases, thena new cross-case model is in order. In this fashion, a case study initiallyframed as a deviant case is likely to be transformed into some other sort ofanalysis.

This feature of the deviant-case study also helps to resolve doubts aboutits representativeness. Evidently, the representativeness of a deviant case isproblematic, since the case in question is, by construction, atypical. How-ever, this problem can be mitigated if the researcher generalizes whateverproposition is provided by the case study to other cases. In a large-Nmodel, this is accomplished by the creation of a variable to represent thenew hypothesis that the case study has identified. This may require some



original coding of cases (in addition to the case under intensive study).However, so long as the underlying information for this coding is avail-able, it should be possible to test the new hypothesis in a cross-case model.If the new variable is successful in explaining the studied case, it should nolonger be deviant; or, at the very least, it will be less deviant. In statisticalterms, its residual will have shrunk. It is now typical, or at least moretypical, and this relieves concerns about possible unrepresentativeness.

Influential Case

Sometimes the choice of a case is motivated solely by the need to verify theassumptions behind a general model of causal relations. Here, the analystattempts to provide a rationale for disregarding a problematic case, or aset of problematic cases. That is to say, she attempts to show why apparentdeviations from the norm are not really deviant, or do not challenge thecore of the theory, once the circumstances of the special case or casesare fully understood. A cross-case analysis may, after all, be marred byseveral classes of problems, including measurement error, specificationerror, errors in establishing proper boundaries for the inference (the scopeof the argument), and stochastic error (fluctuations in the phenomenonunder study that are treated as random, given available theoretical andempirical resources). If poorly fitting cases can be explained away byreference to these kinds of problems, then the theory of interest is thatmuch stronger. This sort of deviant-case analysis answers the question,“What about Case A (or cases of Type A)? How does that (seeminglydisconfirming) case fit the model?”

Because its underlying purpose, as well as the appropriate techniquesfor case identification, is different from that of the deviant-case study,I offer a new term for this method. The influential case is a case thatappears at first glance to invalidate a theory, or at least to cast doubtupon a theory. Possibly, upon closer inspection, it does not. Indeed, itmay end up confirming that theory – perhaps in some slightly alteredform. In this guise, the influential case is the “case that proves the rule.”

A simple version of influential-case analysis involves the confirmationof a key case’s score on some critical dimension. This is essentially aquestion of measurement. Sometimes cases are poorly explained simplybecause they are poorly understood. A close examination of a particularcontext may reveal that an apparently falsifying case has been miscoded.If so, the initial challenge presented by that case to some general theoryhas been obviated.



However, the more usual employment of the influential-case methodculminates in a substantive reinterpretation of the case – perhaps evenof the general model. It is not just a question of measurement. ConsiderThomas Ertman’s study of state building in Western Europe. As summa-rized by Gerardo Munck, this study argues

that the interaction of a) the type of local government during the first period ofstatebuilding, with b) the timing of increases in geopolitical competition, stronglyinfluences the kind of regime and state that emerge. [Ertman] tests this hypoth-esis against the historical experience of Europe and finds that most countries fithis predictions. Denmark, however, is a major exception. In Denmark, sustainedgeopolitical competition began relatively late and local government at the begin-ning of the statebuilding period was generally participatory, which should have ledthe country to develop ‘patrimonial constitutionalism.’ But in fact, it developed‘bureaucratic absolutism.’ Ertman carefully explores the process through whichDenmark came to have a bureaucratic absolutist state and finds that Denmarkhad the early marks of a patrimonial constitutionalist state. However, the countrywas pushed off this developmental path by the influence of German knights, whoentered Denmark and brought with them German institutions of local govern-ment. Ertman then traces the causal process through which these imported insti-tutions pushed Denmark to develop bureaucratic absolutism, concluding that thisdevelopment was caused by a factor well outside his explanatory framework.30

Ertman’s overall framework is confirmed insofar as he has been able toshow, by an in-depth discussion of Denmark, that the causal processesstipulated by the general theory hold even in this apparently disconfirmingcase. Denmark is still deviant, but it is so because of “contingent historicalcircumstances” that are exogenous to the theory.31

The reader will have noted that influential-case analysis is similar todeviant-case analysis. Both focus on outliers, unusual cases (relative to thetheory at hand). However, as we shall see, they focus on different kindsof unusual cases. Moreover, the animating goals of these two researchdesigns are quite different. The influential-case analysis begins with theaim of confirming a general model, while the deviant-case study has theaim of generating a new hypothesis that modifies an existing generalmodel. The confusion between these two case-study types stems fromthe fact that the same case study may fulfill both objectives – qualifying ageneral model and, at the same time, confirming its core hypothesis.

In their study of Roberto Michels’s “iron law of oligarchy,” Lipset,Trow, and Coleman choose to focus on an organization – the International

30 Munck (2004: 118). See also Ertman (1997).31 Ertman (1997: 316).



Typographical Union – that appears to violate the central presupposi-tion.32 The ITU, as noted by one of the authors, has “a long-term two-party system with free elections and frequent turnover in office” and isthus anything but oligarchic.33 Thus, it calls into question Michels’s grandgeneralization about organizational behavior. The authors explain thiscurious result by the extraordinarily high level of education among themembers of this union. Thus, Michels’s law is shown to be valid for mostorganizations, but not all. It is valid with qualifications. Note that therespecification of the original model (in effect, Lipset, Trow, and Cole-man introduce a new control variable or boundary condition) involvesthe exploration of a new hypothesis. In this respect, the use of an influ-ential case to confirm an existing theory is quite similar to the use of adeviant case to unearth a new theory.

Cross-Case TechniqueInfluential cases in regression are those cases that, if counterfactuallyassigned a different value on the dependent variable, would most substan-tially change the resulting estimates. Two quantitative measures of influ-ence are commonly applied in regression diagnostics.34 The first, oftenreferred to as the “leverage” of a case, derives from what is called the hatmatrix.35 Suppose that the scores on the independent variables for all ofthe cases in a regression are represented by the matrix X, which has Nrows (representing each of the N cases) and K + 1 columns (representingthe K independent variables and allowing for a constant). Further, allowY to represent the scores on the dependent variable for all of the cases.Therefore, Y will have N rows and only one column.

Using these symbols, the formula for the hat matrix, H, is as follows:

H = X(XTX)−1XT (5.6)

In this equation, the symbol “T” represents a matrix transpose operation,and the symbol “−1” represents a matrix inverse operation.36 A measure

32 Lipset, Trow, and Coleman (1956).33 Lipset (1959: 70).34 Belsey, Kuh, and Welsch (2004).35 This somewhat curious name derives from the fact that, if the hat matrix is multiplied by

the vector containing values of the dependent variable, the result is the vector of fittedvalues for each case. Typically, the vector of fitted values for the dependent variable isdistinguished from the actual vector of values on the dependent variable by the use ofthe “ˆ” or “hat” symbol. Hence, the hat matrix, which produces the fitted values, can besaid to put the hat on the dependent variable.

36 See Greene (2002) for a brief review.



of the leverage of each case can be derived from the diagonal of the hatmatrix. Specifically, the leverage of case i is given by the number in the(i,i) position in the hat matrix, or Hi,i.37

For any X matrix, the diagonal entries in the hat matrix will automat-ically add up to K + 1. Hence, interpretations of the leverage scores fordifferent cases will necessarily depend on the overall number of cases.Clearly, any case with a score near one is a case with a great deal of lever-age. In most regression situations, however, no case has a score that high.A standard rule of thumb is to pay close attention to cases with a leveragescore higher than 2 (K + 1)/N. Cases with a leverage score above thisvalue are good candidates for influential-case selection.

An interesting feature of the hat matrix is that it does not depend onthe values of the dependent variable. Indeed, the Y vector does not appearin equation 5.6. This means that the measure of leverage derived from thehat matrix is, in effect, a measure of potential influence. It tells us howmuch difference the case would make in the final estimate if it were tohave an unusual score on the dependent variable, but it does not tell ushow much difference each case actually made in the final estimate.

Analysts involved in selecting influential cases will sometimes be inter-ested in measures of potential influence, because such measures are rele-vant in selecting cases when there may be some a priori uncertainty aboutscores on the dependent variable. Much of the information in such casestudies comes from a careful, in-depth measurement of the dependentvariable – which may sometimes be unknown, or only approximatelyknown, before the case study begins. The measure of leverage derivedfrom the hat matrix is appropriate for such situations because it does notrequire actual scores for the dependent variable.

A second commonly discussed measure of influence in statistics isCook’s distance. This statistic is a measure of the extent to which the esti-mates of the β i parameters would change if a given case were omitted fromthe analysis. Because regression analysis typically includes more than oneβ i parameter, a measure of influence requires some method of combiningthe differences in each parameter to produce an overall measure of acase’s influence. The Cook’s distance statistic resolves this dilemma by

37 The discussion here involves the use of the hat matrix in linear regression. Analysts mayalso be interested in situations that do not resemble linear regression problems, e.g.,where the dependent variable is dichotomous or categorical. Sometimes, these situationscan be accommodated within the framework of generalized linear models, which includesits own generalization of the hat matrix (McCullagh and Nelder 1989).



taking a weighted sum of the squared parameter differences associatedwith deleting a specific case. Specifically, the formula for Cook’s distanceis:

(b−i − b)TXTX(b−i − b)(K + 1)MSE

(5.7)

In this formula, b represents all of the parameter estimates from theregression using the whole set of cases, and b-i represents the parameterestimates from the regression that excludes the ith case. X, as above,represents the matrix of independent variables. K is the total number ofindependent variables (not including the constant, which is allowed forin the formula by the use of K + 1). Finally, MSE stands for the meansquared error, which is a measure of the amount of variation in the depen-dent variable not linearly associated with the independent variables.38

This somewhat intimidating mathematical notation gives preciseexpression to the intuitive idea, discussed earlier, of measuring influenceas a weighted sum of the differences that result in each parameter esti-mate when a single case is deleted from the sample. One disadvantage ofthis formula is that it requires a number of extra regressions to be run inorder to compute measures of influence for each case. The overall regres-sion must of course be computed, and then an additional regression, withone case deleted, is required for each case.

Fortunately, matrix-algebraic manipulation demonstrates that theexpression for Cook’s distance given in equation 5.7 is equivalent to thefollowing, computationally much easier expression:

r2i Hi,i

(K + 1)(1 − Hi,i )(5.8)

In this expression, Hi, i refers to the measure of leverage for the ith case,taken from the diagonal of the hat matrix, as already discussed. K onceagain represents the number of independent variables. Finally, r2

i is aspecial, modified version of the ith case’s regression residual, known asthe Studentized residual, which needs to be separately computed.

The Studentized residual is designed so that the residuals for all caseswill have the same variance. If the standard regression residual for case i

38 Specifically, the MSE is found by summing the squared residuals from the full regressionand then dividing by N – K – 1, where N is the number of cases and K is the number ofindependent variables.



is denoted by εi, then the Studentized residual, r2i , can be computed as

follows. (All symbols in this expression are as previously defined.)

ri = εi√MSE(1 − Hi,i )

(5.9)

As can be seen from an inspection of equations 5.8 and 5.9, Cook’s dis-tance for a case depends primarily on two quantities: the size of the regres-sion residual for that case and the leverage for that case. The most influ-ential cases are those with substantial leverage that lie significantly off theregression line.

Cook’s distance for a given case provides a summary of the overalldifference that the decision to include that case makes for the parameterestimates. Cases with a large Cook’s distance contribute quite a lot tothe inferences drawn from the analysis. In this sense, such cases are vitalfor maintaining analytic conclusions. Discovering a significant measure-ment error on the dependent variable or an important omitted variablefor such a case may dramatically revise estimates of the overall relation-ships. Hence, it may be reasonable to select influential cases for in-depthstudy.

To summarize, three statistical concepts have been introduced in thissection. The hat matrix provides a measure of leverage, or potential influ-ence. Based solely on each case’s scores on the independent variables, thehat matrix tells us how much a change in (or a measurement error on)the dependent variable for that case would affect the overall regressionline. Cook’s distance goes further, considering scores on both the indepen-dent and the dependent variables in order to tell us how much the overallregression estimates would be affected if each case were to be droppedfrom the analysis. This produces a measure of how much actual influenceeach case has on the overall regression.

Either the hat matrix or Cook’s distance may serve as an acceptablemeasure of influence for selecting case studies, although the differencesjust discussed must be kept in mind. In the following examples, Cook’s dis-tance will be used as the primary measure of influence because our interestis in whether any particular cases might be influencing the coefficient esti-mates in our democracy-and-development regression. A third concept, theStudentized residual, was introduced as a necessary element in computingCook’s distance. (The hat matrix is, of course, also a necessary ingredientin Cook’s distance.)

Figure 5.6 shows the Cook’s distance scores for each of the countriesin the 1995 per capita GDP and democracy dataset. Most countries have



0 20 40 60 80 100 120

Country code

Coo

k’s

dist

ance

0.0

0.02

0.04

0.06

0.08

0.10

0.12

7574

figure 5.6. Potential influential cases. The Cook’s distance scores for an OLSregression of democracy on logged per capita GDP. The three numbered caseshave high Cook’s distance scores.

quite low scores. The three most serious exceptions to this generalizationare the numbered lines in the figure: Jamaica (74), Japan (75), and Nepal(105). Of these three, Nepal is clearly the most influential by a widemargin. Hence, any study of influential cases would want to start with anin-depth consideration of Nepal.

ConclusionThe use of an influential-case strategy of case selection is limited toinstances in which a researcher has reason to be concerned that her resultsare being driven by one or a few cases. This is most likely to be true insmall to moderate-sized samples. Where N is very large – greater than1,000, let us say – it is extremely unlikely that a small set of cases (muchless an individual case) will play an “influential” role. Of course, theremay be influential sets of cases – for example, countries within a particularcontinent or cultural region, or persons of Irish extraction. Sets of influ-ential observations are often problematic in a time-series cross-sectiondataset where each unit (e.g., country) contains multiple observations(through time) and hence may have a strong influence on aggregate results.Still, the general rule is: the larger the sample, the less important individual



cases are likely to be and, hence, the less likely a researcher is to use hatmatrix and Cook’s distance statistics for purposes of case selection. Inthese instances, it may not matter very much what values individual casesdisplay. (It may of course matter for the purpose of investigating causalmechanisms. However, for this purpose one would not employ influentialstatistics to choose cases.)

Crucial Case

Of all the extant methods of case selection, perhaps the most storied – andcertainly the most controversial – is the crucial-case method, introducedto the social science world several decades ago by Harry Eckstein. Inhis seminal essay, Eckstein describes the crucial case as one “that mustclosely fit a theory if one is to have confidence in the theory’s validity, or,conversely, must not fit equally well any rule contrary to that proposed.”39

A case is “crucial” in a somewhat weaker – but much more common –sense when it is most, or least, likely to fulfill a theoretical prediction. A“most-likely” case is one that, on all dimensions except the dimensionof theoretical interest, is predicted to achieve a certain outcome, and yetdoes not. It is therefore used to disconfirm a theory. A “least-likely” case isone that, on all dimensions except the dimension of theoretical interest, ispredicted not to achieve a certain outcome, and yet does so. It is thereforeused to confirm a theory. In all formulations, the crucial case offers amost-difficult test for an argument, and hence provides what is perhapsthe strongest sort of evidence possible in a nonexperimental, single-casesetting.

Since the publication of Eckstein’s influential essay, the crucial-caseapproach has been claimed in a multitude of studies across several socialscience disciplines and has come to be recognized as a staple of thecase study method.40 Yet the idea of any single case playing a crucial(or “critical”) role is not widely accepted among most methodologists.41

(Even its progenitor seems to have had doubts.)Unfortunately, discussion of this method has focused misleadingly on

what are presumed to be largely inductive issues. Are there good crucial

39 Eckstein (1975: 118).40 For examples of the crucial-case method, see Bennett, Lepgold, and Unger (1994); Desch

(2002); Goodin and Smitsman (2000); Kemp (1986); and Reilly and Phillpot (2003).For general discussion, see George and Bennett (2005); Levy (2002a); and Stinchcombe(1968: 24–8).

41 See, e.g., Sekhon (2004).



cases out there in the empirical world? Have social scientists done a goodjob in identifying them? Yet the practicability of this method rests onissues that are largely deductive in nature, as we shall see.

The Confirmatory (Least-Likely) Crucial CaseLet us begin with the confirmatory (a.k.a. least-likely) crucial case. Theimplicit logic of this research design may be summarized as follows. Givena set of facts, we are asked to contemplate the probability that a given the-ory is true. While the facts matter, to be sure, the effectiveness of this sortof research also rests upon the formal properties of the theory in question.Specifically, the degree to which a theory is amenable to confirmation iscontingent upon how many predictions can be derived from the theoryand on how “risky” each individual prediction is. In Popper’s words,

Confirmations should count only if they are the result of risky predictions; thatis to say, if, unenlightened by the theory in question, we should have expectedan event which was incompatible with the theory – an event which would haverefuted the theory. Every ‘good’ scientific theory is a prohibition; it forbids certainthings to happen. The more a theory forbids, the better it is.42

A risky prediction is therefore one that is highly precise and determi-nate, and thus unlikely to be explainable by other causal factors (externalto the theory of interest) or through stochastic processes. A theory pro-duces many such predictions if it is fully elaborated, issuing predictionsnot only on the central outcome of interest but also on specific causalmechanisms, and if it is broad in purview. (The notion of riskiness may beconceptualized within the Popperian lexicon as degrees of falsifiability.)

These points can also be articulated in Bayesian terms. Colin Howsonand Peter Urbach explain: “The degree to which h [a hypothesis] is con-firmed by e [a set of evidence] depends . . . on the extent to which P(e|h)exceeds P(e), that is, on how much more probable e is relative to thehypothesis and background assumptions than it is relative just to back-ground assumptions.” Again, “confirmation is correlated with how muchmore probable the evidence is if the hypothesis is true than if it is false.”43

Thus, the stranger the prediction offered by a theory – relative to whatwe would normally expect – the greater the degree of confirmation thatwill be afforded by the evidence. As an intuitive example, Howson andUrbach offer the following:

42 Popper (1963: 36). See also Popper (1934/1968).43 Howson and Urbach (1989: 86).



If a soothsayer predicts that you will meet a dark stranger sometime and you do infact, your faith in his powers of precognition would not be much enhanced: youwould probably continue to think his predictions were just the result of guesswork.However, if the prediction also gave the correct number of hairs on the head ofthat stranger, your previous scepticism would no doubt be severely shaken.44

While these Popperian/Bayesian insights45 are relevant to all empiri-cal research designs, they are especially relevant to case study researchdesigns, for in these settings a single case (or, at most, a small numberof cases) is required to bear a heavy burden of proof. It should be nosurprise, therefore, that Popper’s idea of “riskiness” was appropriated bycase study researchers like Harry Eckstein to validate the enterprise ofsingle-case analysis. (Although Eckstein does not cite Popper, the intel-lectual lineage is clear.) Riskiness, here, is analogous to what is usuallyreferred to as a “most-difficult” research design, which in a case studyresearch design would be understood as a least-likely case. Note also thatthe distinction between a must-fit case and a least-likely case – that, inthe event, actually does fit the terms of a theory – is a matter of degree.Cases are more or less crucial for confirming theories. The point is that,in some circumstances, the riskiness of the theory may compensate for apaucity of empirical evidence.

The crucial-case research design is, perforce, a highly deductiveenterprise; much depends on the quality of the theory under investiga-tion. It follows that the theories most amenable to crucial-case analysisare those that are lawlike in their precision, degree of elaboration, con-sistency, and scope. The more a theory attains the status of a causal law,the easier it will be to confirm, or to disconfirm, with a single case.

Indeed, risky predictions are common in natural science fields suchas physics, which in turn served as the template for the deductive-nomological (“covering-law”) model of science that influenced Ecksteinand others in the postwar decades.46 A frequently cited example is thefirst important empirical demonstration of the theory of relativity, whichtook the form of a single-event prediction on the occasion of the May29, 1919, solar eclipse. Stephen Van Evera describes the impact of thisprediction on the validation of Einstein’s theory.

44 Ibid.45 A third position, which purports to be neither Popperian nor Bayesian, has been articu-

lated by Mayo (1996: Chapter 6). From this perspective, the same idea is articulated asa matter of “severe tests.”

46 See, e.g., Hempel (1942).



Einstein’s theory predicted that gravity would bend the path of light toward agravity source by a specific amount. Hence it predicted that during a solar eclipsestars near the sun would appear displaced – stars actually behind the sun wouldappear next to it, and stars lying next to the sun would appear farther from it – andit predicted the amount of apparent displacement. No other theory made thesepredictions. The passage of this one single-case-study test brought the theory wideacceptance because the tested predictions were unique – there was no plausiblecompeting explanation for the predicted result – hence the passed test was verystrong.47

The strength of this test is the extraordinary fit between the theory and aset of facts found in a single case, and the corresponding lack of fit betweenall other theories and this set of facts. Einstein offered an explanation ofa particular set of anomalous findings that no other existing theory couldmake sense of. Of course, one must assume that there was no – or limited –measurement error. And one must assume that the phenomenon of inter-est is largely invariant; light does not bend differently at different timesand places (except in ways that can be understood through the theory ofrelativity). And one must assume, finally, that the theory itself makes senseon other grounds (other than the case of special interest); it is a plausiblegeneral theory. If one is willing to accept these a priori assumptions, thenthe 1919 “case study” provides a very strong confirmation of the theory.It is difficult to imagine a stronger proof of the theory from within anobservational (nonexperimental) setting.

In social science settings, by contrast, one does not commonly findsingle-case studies offering knock-out evidence for a theory. This is, inmy view, largely a product of the looseness (the underspecification) ofmost social science theories. George and Bennett point out that while thethesis of the democratic peace is as close to a “law” as social sciencehas yet seen, it cannot be confirmed (or refuted) by looking at specificcausal mechanisms because the causal pathways mandated by the theoryare multiple and diverse. Under the circumstances, no single-case test canoffer strong confirmation of the theory (though, as we shall discuss, thetheory may be disconfirmed with a single case).48

However, if one adopts a softer version of the crucial-case method –the least-likely (most difficult) case – then possibilities abound. Lily Tsai’sinvestigation of governance at the village level in China employs severalin-depth case studies of villages that are chosen (in part) because of their

47 Van Evera (1997: 66–7). See also Eckstein (1975) and Popper (1963).48 George and Bennett (2005: 209).



least-likely status relative to the theory of interest. Tsai’s hypothesis is thatvillages with greater social solidarity (based on preexisting religious orfamilial networks) will develop a higher level of social trust and mutualobligation and, as a result, will experience better governance. Crucialcases, therefore, are villages that evidence a high level of social solidaritybut that, along other dimensions, would be judged least-likely to developgood governance – that is, they are poor, isolated, and lack democraticinstitutions or accountability mechanisms from above. “Li Settlement,”in Fujian province, is such a case. The fact that this impoverished villagenonetheless boasts an impressive set of infrastructural accomplishmentssuch as paved roads with drainage ditches (a rarity in rural China) sug-gests that something rather unusual is going on here. Because her case iscarefully chosen to eliminate rival explanations, Tsai’s conclusions aboutthe special role of social solidarity are difficult to gainsay. How else wouldone explain this otherwise anomalous result? This is the strength of theleast-likely case, where all other plausible explanations for an outcomehave been mitigated.49

Jack Levy refers to this, evocatively, as a “Sinatra inference”: if it canmake it here, it can make it anywhere.50 Thus, if social solidarity hasthe hypothesized effect in Li Settlement, it should have the same effect inmore propitious settings (e.g., where there is greater economic surplus).The same implicit logic informs many case study analyses where the intentof the study is to confirm a hypothesis on the basis of a single case (with-out extensive cross-case analysis). Indeed, I suspect that, implicitly, mostcase study work that focuses on a single case and is not nested withina cross-case analysis relies largely on the logic of the least-likely case.Rarely is this logic made explicit, except perhaps in a passing phrase ortwo. Yet the deductive logic of the “risky” prediction may in fact be cen-tral to the case study enterprise. Whether a case study is convincing ornot often rests on the reader’s evaluation of how strong the evidence foran argument might be, and this in turn – wherever cross-case evidence islimited and no manipulated treatment can be devised – rests upon an esti-mation of the degree of “fit” between a theory and the evidence at hand, asdiscussed.

49 Tsai (2007). It should be noted that Tsai’s conclusions do not rest solely on this crucialcase. Indeed, she employs a broad range of methodological tools, encompassing casestudy and cross-case methods.

50 Levy (2002a: 144). See also Khong (1992: 49); Sagan (1995: 49); and Shafer (1988:14–6).



The Disconfirmatory (Most-Likely) Crucial CaseA central Popperian insight is that it is easier to disconfirm an inferencethan to confirm that same inference. (Indeed, Popper doubted that anyinference could be fully confirmed, and for this reason preferred the term“corroborate.”) This is particularly true of case study research designs,where evidence is limited to one or several cases. The key proviso is thatthe theory under investigation must take a consistent (a.k.a. invariant,deterministic) form, even if its predictions are not terrifically precise, wellelaborated, or broad.

As it happens, there are a fair number of invariant propositions float-ing around the social science disciplines.51 In Chapter Three, we discussedan older theory that stipulated that political stability would occur onlyin countries that are relatively homogeneous, or where existing hetero-geneities are mitigated by cross-cutting cleavages.52 Arend Lijphart’s studyof the Netherlands, a peaceful country with reinforcing social cleavages, iscommonly viewed as refuting this theory on the basis of a single in-depthcase analysis.53

Heretofore, I have treated causal factors as dichotomous. Countrieshave either reinforcing or cross-cutting cleavages, and they have regimesthat are either peaceful or conflictual. Evidently, these sorts of parametersare often matters of degree. In this reading of the theory, cases are moreor less crucial. Accordingly, the most useful – that is, most crucial – casefor Lijphart’s purpose is one that has the most segregated social groupsand the most peaceful and democratic track record. In these respects,the Netherlands was a very good choice. Indeed, the degree of disconfir-mation offered by this case study is probably greater than the degree ofdisconfirmation that might have been provided by another case, such asIndia or Papua New Guinea – countries where social peace has not alwaysbeen secure. The point is that where variables are continuous rather thandichotomous, it is possible to evaluate potential cases in terms of theirdegree of crucialness.

Note that when disconfirming a causal argument, background causalfactors are irrelevant (except as they might affect the classification of thecase within the population of an inference). It does not matter how the

51 Goertz and Levy (forthcoming); Goertz and Starr (2003).52 Almond (1956); Bentley (1908/1967); Lipset (1960/1963); Truman (1951).53 Lijphart (1968). See also discussions in Eckstein (1975) and Lijphart (1969). For addi-

tional examples of case studies disconfirming general propositions of a deterministicnature, see Allen (1965); Lipset, Trow, and Coleman (1956); Njolstad (1990); Reilly(2000/2001); and the discussions in Dion (1998) and Rogowski (1995).



Netherlands, India, and Papua New Guinea score on other factors thataffect democracy and social peace.

Granted, it may be questioned whether presumed invariant theories arereally invariant; perhaps they are better understood as probabilistic. Per-haps, that is, the theory of cross-cutting cleavages is still true, probabilisti-cally, despite the apparent Dutch exception. Or perhaps the theory is stilltrue, deterministically, within a subset of cases that does not include theNetherlands. (This sort of claim seems unlikely in this particular instance,but it is quite plausible in many others.) Or perhaps the theory is in needof reframing; it is true, deterministically, but applies only to cross-cuttingethnic/racial cleavages, not to cleavages that are primarily religious. Onemay quibble over what it means to “disconfirm” a theory. The point isthat the crucial case has, in all these circumstances, provided importantupdating of a theoretical prior.

ConclusionIn this section, I have argued that the degree to which crucial cases canprovide decisive confirmation or disconfirmation of a theory is in largepart a product of the structure of the theory to be tested. It is a deductivematter rather than an inductive matter, strictly speaking. In this respect,a “positivist” orientation toward the work of social science may lead to agreater appreciation of the case study format – not a denigration of thatformat, as is usually supposed. Those who, with Eckstein, embrace thenotion of covering laws are likely to be attracted to the idea of cases thatare crucial. By the same token, those who are impressed by the irregularityand complexity of social behavior are unlikely to be persuaded by crucial-case studies, except as a method of disconfirming absurdly rigid causallaws.

I have shown, relatedly, that it is almost always easier to disconfirma theory than to confirm it with a single case. Thus, a theory that isunderstood to be deterministic may be disconfirmed by a case study, prop-erly chosen. This is the most common employment of the crucial-casemethod in social science settings.

Note that the crucial-case method of case selection cannot be employedin a large-N context. This is because the method of selection would renderthe case study redundant. Once one identifies the relevant parameters andthe scores of all cases on those parameters, one has in effect constructeda cross-case model that will, by itself, confirm or disconfirm the theory inquestion. The case study is thenceforth irrelevant, at least as a means ofconfirmation or disconfirmation. It remains highly relevant as a means of



exploring causal mechanisms, of course. However, because this objectiveis quite different from that which is usually associated with the term, Ienlist a new term for this technique.

Pathway Case

One of the most important functions of case study research is the elucida-tion of causal mechanisms. This is well established (see Chapter Three).But what sort of case is most useful for this purpose? Although all casestudies presumably shed light on causal mechanisms, not all cases areequally transparent. In situations where a causal hypothesis is clear andhas already been confirmed by cross-case analysis, researchers are welladvised to focus on a case where the causal effect of one factor canbe isolated from other potentially confounding factors. I shall call thisa pathway case to indicate its uniquely penetrating insight into causalmechanisms.

To clarify, the pathway case exists only in circumstances where cross-case covariational patterns are well studied but where the mechanismlinking X1 and Y remains dim. Because the pathway case builds on priorcross-case analysis, the problem of case selection must be situated withinthat sample. There is no stand-alone pathway case. Thus, the followingdiscussion focuses on how to select one (or a few) cases from a cross-casesample.

Cross-Case Technique with Binary VariablesThe logic of the pathway case is clearest in situations of causal sufficiency –where a causal factor of interest, X1, is sufficient by itself (though per-haps not necessary) to cause a particular outcome, Y, understood as aunidirectional or asymmetric casual relationship. The other causes ofY, about which we need make no assumptions, are designated as avector, X2.

Note that wherever various causal factors are deemed to be substi-tutable for one another, each factor is conceptualized (individually) assufficient.54 Situations of causal equifinality presume causal sufficiencyon the part of each factor or set of conjoint factors. The QCA technique,for example, presumes causal sufficiency for each of the designated causalpaths.

54 Braumoeller (2003).



Consider the following examples culled by Bear Braumoeller anddrawn from diverse fields of political science.55 The decision to seek analliance is motivated by the search for either autonomy or security.56 Con-quest is prevented by either deterrence or defense.57 Civilian interventionin military affairs is caused by either political isolation or geographicalencirclement.58 War is the product of miscalculation or loss of control.59

Nonvoting is caused by ignorance, indifference, dissatisfaction, or inac-tivity.60 Voting decisions are influenced either by high levels of informa-tion or by the use of candidate gender as a proxy for social information.61

Democratization comes about through leadership-initiated reform, a con-trolled opening to opposition, or the collapse of an authoritarian regime.62

These, and many other, social science arguments take the form of causalsubstitutability – multiple paths to a given outcome.

For heuristic purposes, it will be helpful to pursue one of these exam-ples in greater detail. For consistency, I focus on the last of the exemplars –democratization. The literature, according to Braumoeller, identifies threemain avenues of democratization (there may be more, but for present pur-poses let us assume that the universe is limited to three). The case studyformat constrains us to analyze one at a time, so let us limit our scope to thefirst one – leadership-initiated reform. So considered, a causal-pathwaycase would be one with the following features: (a) democratization,(b) leadership-initiated reform, (c) no controlled opening to the opposi-tion, (d) no collapse of the previous authoritarian regime, and (e) no otherextraneous factors that might affect the process of democratization. In acase of this type, the causal mechanisms by which leadership-initiatedreform may lead to democratization will be easiest to study. Note that itis not necessary to assume that leadership-initiated reform always leadsto democratization; it may or may not be a deterministic cause. But it isnecessary to assume that leadership-initiated reform can sometimes leadto democratization. This covariational assumption about the relationship

55 Ibid. My chosen examples are limited to those that might plausibly be modeled withdichotomous variables. For further discussion and additional examples, see Most andStarr (1984) and Cioffi-Revilla and Starr (1995).

56 Morrow (1991: 905).57 Schelling (1966: 78).58 Posen (1984: 79).59 Levy (1983: 86).60 Ragsdale and Rusk (1993: 723–4).61 McDermott (1997).62 Colomer (1991).



table 5.2. Pathway case with dichotomous causal factors

X1 X2 Y A 1 1B 0 0 C 0 1 1D 0 0 1E 1 0 0F 1 1 0G 0 1 0

Casetypes

H 1 0 1

10

X1 = the variable of theoretical interest. X2 = a vector of controls(a score of zero indicates that all control variables have a score of zero,while a score of one indicates that all control variables have a scoreof one). Y = the outcome of interest. A–H = case types (the N foreach case type is indeterminate). H = pathway case. Sample size =indeterminate.Assumptions: (a) all variables can be coded dichotomously; (b) allindependent variables are positively correlated with Y in the generalcase; (c) X1 is (at least sometimes) a sufficient cause of Y.

between X1 and Y is presumably sustained by the cross-case evidence (ifit is not, there is no justification for a pathway case study).

Now let us move from these examples to a general-purpose model.For heuristic purposes, let us presume that all variables in that model aredichotomous (coded as zero or one) and that the model is complete (allcauses of Y are included). All causal relationships will be coded so as tobe positive: X1 and Y covary as do X2 and Y. This allows us to visualizea range of possible combinations at a glance.

Recall that the pathway case is always focused, by definition, on asingle causal factor, denoted X1. (The researcher’s focus may shift to othercausal factors, but may focus only on one causal factor at a time.) Inthis scenario, and regardless of how many additional causes of Y theremight be (denoted X2, a vector of controls), there are only eight relevantcase types, as illustrated in Table 5.2. Identifying these case types is arelatively simple matter, and can be accomplished in a small-N sample bythe construction of a truth table (modeled after Table 5.2) or in a large-Nsample by the use of cross-tabs.

Note that the total number of combinations of values depends on thenumber of control variables, which we have represented with a singlevector, X2. If this vector consists of a single variable, then there are onlyeight case types. If this vector consists of two variables (X2a, X2b), then the



total number of possible combinations increases from eight (23) to sixteen(24), and so forth. However, none of these combinations is relevant forpresent purposes except those where X2a and X2b have the same value(zero or one). “Mixed” cases are not causal pathway cases, for reasonsthat should become clear.

The pathway case, following the logic of the crucial case, is one wherethe causal factor of interest, X1, correctly predicts Y’s positive value(Y = 1) while all other possible causes of Y (represented by the vector,X2) make “wrong” predictions. If X1 is – at least in some circumstances –a sufficient cause of Y, then it is these sorts of cases that should be mostuseful for tracing causal mechanisms. There is only one such case inTable 5.2 – H. In all other cases, the mechanism running from X1 toY would be difficult to discern, because the outcome to be explained doesnot occur (Y = 0), because X1 and Y are not correlated in the usual way(violating the terms of our hypothesis), or because other confounding fac-tors (X2) intrude. In case A, for example, the positive value on Y could bea product of X1 or X2. Consequently, an in-depth examination of casesA–G is not likely to be very revealing.

Keep in mind that because we already know from our cross-case exam-ination what the general causal relationships are, we know (prior to thecase study investigation) what constitutes a correct or incorrect predic-tion. In the crucial-case method, by contrast, these expectations are deduc-tive rather than empirical. This is what differentiates the two methods.And this is why the causal-pathway case is useful principally for eluci-dating causal mechanisms rather than for verifying or falsifying generalpropositions (which are already apparent from the cross-case evidence).63

Now let us complicate matters a bit by imagining a scenario in which atleast some of these substitutable causes are conjoint (a.k.a. conjunctural).That is, several combinations of factors – Xa + Xb or Xc + Xd – aresufficient to produce the outcome, Y. This is known in philosophical circlesas an INUS condition,64 and it is the pattern of causation assumed in most

63 Of course, we should leave open the possibility that an investigation of causal mechanismsmight invalidate a general claim, if that claim is utterly contingent upon a specific setof causal mechanisms and the case study shows that no such mechanisms are present.However, this is rather unlikely in most social science settings. Usually, the result of sucha finding will be a reformulation of the causal processes by which X1 causes Y – or,alternatively, a realization that the case under investigation is aberrant (atypical of thegeneral population of cases).

64 An INUS condition refers to an Insufficient but Necessary part of a condition which isitself Unnecessary but Sufficient for a particular result. Thus, when one identifies a shortcircuit as the “cause” of a fire, one is saying, in effect, that the fire was caused by a short



QCA (Qualitative Comparative Analysis) models.65 Here, everything thathas been said so far must be adjusted so that X1 refers to a set of causes(e.g., Xa + Xb) and X2 refers to a vector of sets (e.g., Xc + Xd, Xe +Xf, Xg + Xh, . . . ). The scoring of all these variables makes matters moredifficult than in the previous set of examples. However, the logical task isidentical, and can be accomplished in a similar fashion, that is, in small-Ndatasets with truth tables and in large-N datasets with cross-tabs. CaseH now refers to a conjunction of causes, but it is still the only possiblepathway case.

Cross-Case Technique with Continuous VariablesFinally, we must tackle the most complicated scenario – when all (or most)variables of concern to the model are continuous, rather than dichoto-mous. Here, the job of case selection is considerably more complex, forcausal “sufficiency” (in the usual sense) cannot be invoked. It is no longerplausible to assume that a given cause can be entirely partitioned, that is,that all rival factors can be eliminated. Even so, the search for a pathwaycase may be viable.

What we are looking for in this scenario is a case that satisfies twocriteria: (1) it is not an outlier (or at least not an extreme outlier) in thegeneral model, and (2) its score on the outcome (Y) is strongly influencedby the theoretical variable of interest (X1), taking all other factors intoaccount (X2). In this sort of case it should be easiest to identify the causalmechanisms that lie between X1 and Y.

In a large-N sample, these two desiderata may be judged by a carefulattention to the residuals attached to each case. Recall that the questionof deviance, which we have discussed in previous sections, is a matter ofdegree. Cases are more or less typical/deviant relative to a general model,as judged by the size of their residuals. It is easy enough to exclude caseswith very high residuals (e.g., standardized residual > | 2 |). For cases thatlie closer to their predicted value, small differences in the size of residualsmay not matter so much. But, ceteris paribus, one would prefer a casethat lies closer to the regression line.

circuit in conjunction with some other background factors (e.g., oxygen) that were alsonecessary to that outcome. But one is not implying that a short circuit was necessary tothat fire, which might have been (under different circumstances) caused by other factors.See Mackie (1965/1993).

65 Ragin (2000).



Achieving the second desideratum requires a bit of manipulation. Inorder to determine which (non-outlier) cases are most strongly affectedby X1, given all the other parameters in the model, one must compare thesize of the residuals (their absolute value) for each case in a reduced-formmodel, Y = Constant + X2 + Resreduced, to the size of the residuals foreach case in a full model, Y = Constant + X2 + X1 + Resfull. The pathwaycase is that case, or set of cases, that shows the greatest difference betweenthe residuals for the reduced-form model and the full model (�Residual).Thus,

Pathway = |Resreduced − Resfull|, if |Resreduced| > |Resfull| (5.10)

Note that the residual for a case must be smaller in the full model than inthe reduced-form model; otherwise, the addition of the variable of interest(X1) pulls the case away from the regression line. We want to find a casewhere the addition of X1 pushes the case toward the regression line, thatis, it helps to “explain” the case.

As an example, let us suppose that we are interested in exploringthe effect of mineral wealth on the prospects for democracy in a soci-ety. According to a good deal of work on this subject, countries with abounty of natural resources – particularly oil – are less likely to democra-tize (or, once having undergone a democratic transition, are more likely torevert to authoritarian rule).66 The cross-country evidence is robust. Yet,as is often the case, causal mechanisms remain rather obscure. Considerthe following list of possible causal pathways, summarized by MichaelRoss:

A ‘rentier effect’ . . . suggests that resources rich governments use low tax ratesand patronage to relieve pressures for greater accountability; a ‘repressioneffect’ . . . argues that resource wealth retards democratization by enabling gov-ernments to boost their funding for internal security; and a ‘modernizationeffect’ . . . holds that growth based on the export of oil and minerals fails to bringabout the social and cultural changes that tend to produce democratic govern-ment.67

Are all three causal mechanisms at work? Although Ross attempts to testthese factors in a large-N cross-country setting, his answers remain rather

66 Barro (1999), Humphreys (2005); Ross (2001).67 Ross (2001: 327–8).



speculative.68 Let us see how this might be handled by a pathway-caseapproach.

The factor of theoretical interest, oil wealth, may be operationalizedas per capita oil production (barrels of oil produced, divided by the totalpopulation of a country).69 As previously, we measure democracy with acontinuous variable coded from −10 (most authoritarian) to +10 (mostdemocratic). Additional factors in the model include GDP per capita(logged), Muslims (as percent of the population), European language (per-cent speaking a European language), and ethnic fractionalization (1 −likelihood of two randomly chosen individuals belonging to the sameethnic group).70 These are regarded as background variables (X2) thatmay affect a country’s propensity to democratize. The full model, limitedto 1995 (as in previous analyses), is as follows:

Democracy = −3.71 Constant + 1.258 GDP (5.11)

+−.075 Muslim + 1.843 European

+−2.093 Ethnic fract +− 7.662 Oil

R2adj = .450 (N = 149)

The reduced-form model is identical except that the variable of theoreticalinterest, Oil, is removed.

Democracy = −.831 Constant + .909 GDP (5.12)

+−.086 Muslim + 2.242 European

+−3.023 Ethnic fract

R2adj = .428 (N = 149)

What does a comparison of the residuals across equations 5.11 and5.12 reveal? Table 5.3 displays the highest �Residual cases. Several of

68 Ross tests these various causal mechanisms with cross-country data, employing variousproxies for these concepts in the benchmark model and observing the effect of these –presumably intermediary – effects on the main variable of interest (oil resources). Thisis a good example of how cross-case evidence can be mustered to shed light on causalmechanisms; one is not limited to case study formats, as discussed in Chapter Three. Still,as Ross notes (2001: 356), these tests are by no means definitive. Indeed, the coefficienton the key oil variable remains fairly constant, except in circumstances where the sampleis severely constrained.

69 Derived from Humphreys (2005).70 GDPpc data are from World Bank (2003). Muslims and European language are coded

by the author. Ethnic fractionalization is drawn from Alesina et al. (2003).



table 5.3. Possible pathway cases where variables are scalar andassumptions probabilistic

Country Resreduced Resfull ∆Residual

Iran −.282 −.456 .175Turkmenistan −1.220 −1.398 .178Mauritania −.076 −.255 .179Turkey 2.261 2.069 .192Switzerland .177 −.028 .205Venezuela .148 .355 −.207Belgium .518 .310 .208Morocco −.540 −.776 .236Jordan .382 .142 .240Djibouti −.451 −.696 .245Bahrain −1.411 −1.673 .262Luxembourg .559 .291 .269Singapore −1.593 −1.864 .271Oman −1.270 −.981 −.289Gabon −1.743 −1.418 −.325Saudi Arabia −1.681 −1.253 −.428Norway .315 1.285 −.971United Arab Emirates −1.256 −.081 −1.175Kuwait −1.007 .925 −1.932

Resreduced = the standardized residual for a case obtained from the reduced model(without Oil) – equation 5.12.Resfull = the standardized residual for a case obtained from the full model (withOil) – equation 5.11.�Residual = Resreduced – Resfull. Listed in order of absolute value.

these may be summarily removed from consideration by virtue of thefact that |Resreduced|<|Resfull|. Thus, we see that the inclusion of Oilincreases the residual for Norway; this case is apparently better explainedwithout the inclusion of the variable of theoretical interest. Needless tosay, this is not a good case to explore if we wish to examine the causalmechanisms that lie between natural resource wealth and democracy. (Itmight, however, be a good case for model diagnostics, as discussed in theprevious section on influential cases.)

Among cases where the residual declines from the reduced to the fullmodel, several are clear-cut favorites as pathway cases. The United ArabEmirates and Kuwait have the highest �Residual values and also havefairly modest residuals in the full model (Resfull), signifying that thesecases are not extreme outliers; indeed, according to the parameters of thismodel, the United Arab Emirates would be regarded as a typical case. The



analysis suggests, therefore, that researchers seeking to explore the effectof oil wealth on regime type might do well to focus on these two cases,since their patterns of democracy cannot be well explained by other fac-tors such as, economic development, religion, European influence, or eth-nic fractionalization. The presence of oil wealth in these countries wouldappear to have a strong independent effect on the prospects for democra-tization in these countries, an effect that is well modeled by our generaltheory and by the available cross-case evidence. And this effect shouldbe interpretable in a case-study format – more interpretable, at any rate,than it would be in other cases.

ConclusionThe logic of causal “elimination” is much more compelling where vari-ables are dichotomous and where causal sufficiency can be assumed (X1 issufficient by itself, at least in some circumstances, to cause Y). Where vari-ables are continuous the strategy of the pathway case is more dubious, forpotentially confounding causal factors (X2) cannot be neatly partitioned.Even so, this discussion has shown why the selection of a pathway case isa logical approach to case study analysis in many circumstances.

The exceptions may be briefly noted. Sometimes, where all variablesin a model are dichotomous, there are no pathway cases, that is, no casesof type H (in Table 5.2). This is known as the “empty cell” problem, or aproblem of severe causal multicollinearity. The universe of observationaldata does not always oblige us with cases that allow us to test a givenhypothesis independently of all others.

Where variables are continuous, the analogous problem is that of acausal variable of interest (X1) that has only minimal effects on the out-come of interest. That is, its role in the general model is quite minor (asjudged by its standardized coefficient or by F-tests comparing the reduced-form model and the full model). In these situations, the only cases thatare strongly affected by X1 – if there are any at all – may be extremeoutliers, and these sorts of cases are not properly regarded as providingconfirmatory evidence for a proposition, for reasons that are abundantlyclear by now.

Finally, it must be underlined that the identification of a causal-pathwaycase does not obviate the utility of exploring other cases. However, thissort of multicase investigation moves beyond the logic of the causal path-way case, underlining a point that we shall return to in the concluding



section of the chapter: case-selection procedures often combine differentlogics.

Despite the technical nature of this discussion, it should be noted thatwhen researchers refer to a particular case as an “example” of a broaderphenomenon, they are often referring to a pathway case. This sort ofcase illustrates the causal relationship of interest in a particularly vividmanner, and therefore may be regarded as a common trope among casestudy researchers.

Most-Similar Case

The most-similar method, unlike the previous methods, employs a mini-mum of two cases.71 In its purest form, the chosen pair of cases is similarin all respects except the variable(s) of interest.

If the study is exploratory (i.e., hypothesis-generating), the researcherlooks for cases that differ on the outcome of theoretical interest but aresimilar on various factors that might have contributed to that outcome, asillustrated in Table 5.4 (A). This is a common form of case selection at theinitial stage of research. Often, fruitful analysis begins with an apparentanomaly: two cases are apparently quite similar, and yet demonstratesurprisingly different outcomes. The hope is that intensive study of thesecases will reveal one – or at most several – factors that differ across thesecases. These differing factors (X1) are the putative causes.

Sometimes, a researcher begins with a strong hypothesis, in which caseher research design is confirmatory (hypothesis-testing) from the get-go.That is, she strives to identify cases that exhibit different scores on thefactor of interest and similar scores on all other possible causal factors,as illustrated in the second (hypothesis-testing) diagram in Table 5.4 (B).If she discovers such a case, it is regarded as providing confirmatory evi-dence for the proposition, as well as fodder for an exploration of causalmechanisms.

The point is that the purpose of a most-similar research design,and hence its basic set-up, may change as a researcher moves from anexploratory to a confirmatory mode of analysis. However, regardless of

71 Sometimes the most-similar method is known as the “method of difference,” afterits inventor (Mill 1843/1872). For later treatments see Cohen and Nagel (1934);Eggan (1954); Gerring (2001: Chapter 9); Lijphart (1971, 1975); Meckstroth (1975);Przeworski and Teune (1970); and Skocpol and Somers (1980).



table 5.4. Most-similar analysis with two case types

(A) Hypothesis-generating (Y-centered):

X1 X2 Y

A ? 0 1Case types B ? 0 0

(B) Hypothesis-testing (X1/Y-centered): X1 X2 Y

A 1 0 ? Case types B 0 0 ?

X1 = the variable of theoretical interest. X2 = a vector ofcontrols. Y = the outcome of interest.

where one begins, the results, when published, look like a hypothesis-testing research design. Question marks have been removed: (A) becomes(B) in Table 5.4. Consequently, the notion of a “most-similar” analysis isusually understood as a tool for understanding a specific X1/Y relation-ship.

As an example, let us consider Leon Epstein’s classic study of partycohesion, which focuses on two similar countries, the United Statesand Canada. Canada has highly disciplined parties whose members votetogether on the floor of the House of Commons, while the United Stateshas weak, undisciplined parties whose members often defect on floor votesin Congress. In explaining these divergent outcomes, persistent over manyyears, Epstein first discusses possible causal factors that are held more orless constant across the two cases. Both the United States and Canadainherited English political cultures; both have large territories and het-erogeneous populations; both are federal; and both have a fairly looseparty structures with strong regional bases and a weak center. These arethe “control” variables (X2). Where they differ is in one constitutionalfeature: Canada is parliamentary, while the United States is presidential.And it is this institutional difference that Epstein identifies as the differ-entiating cause (X1).72

Several caveats apply to any most-similar analysis (in addition tothe usual set of assumptions applying to all case study analysis). First,

72 For further examples of the most-similar method, see Brenner (1976); Hamilton (1977);Lipset (1968); Miguel (2004); Moulder (1977); and Posner (2004).



one must code cases dichotomously (high/low, present/absent). This isstraightforward if the underlying variables are also dichotomous (e.g.,federal/unitary). However, it is often the case that variables of concernin the model are continuous (e.g., party cohesion). In this setting, theresearcher must “dichotomize” the scoring of cases so as to simplify thetwo-case analysis. This is relatively unproblematic if the actual scores onthis dimension are quite different (on X1 and Y) or virtually identical(on X2). Unfortunately, the empirical universe does not always oblige therequirements of Millean-style analysis, and in these instances the logic ofmost-similar comparison becomes questionable.

Some flexibility is admissible on the vector of controls (X2) that are“held constant” across the cases. Nonidentity is tolerable if the deviationruns counter to the predicted hypothesis. For example, Epstein describesboth the United States and Canada as having strong regional bases ofpower, a factor that is probably more significant in recent Canadian his-tory than in recent American history. However, because regional bases ofpower should lead to weaker parties, rather than to stronger parties, thiselement of nonidentity does not challenge Epstein’s conclusions. Indeed, itsets up a most-difficult research scenario, as discussed earlier. At the sametime, Epstein’s description of Canadian and American parties as “loose”might be questioned. Arguably, American parties, dominated in the lattertwentieth century by direct primaries (open to all who declare themselvesa member of a party and, in some states, even to those who are mem-bers of the opposing party), are considerably more diffuse than Canadianparties. The problem of coding continuous variables in a dichotomousmanner is threatening to any most-similar analysis.

In one respect, however, the requirements for case control are not sostringent. Specifically, it is not usually necessary to measure control vari-ables (at least not with a high degree of precision) in order to control forthem. If two countries can be assumed to have similar cultural heritages,one needn’t worry about constructing variables to measure that heritage.One can simply assert that, whatever they are, they are more or less con-stant across the two cases. This is similar to the technique employed in arandomized experiment, where the researcher typically does not attemptto measure all the factors that might affect the causal relationship of inter-est. She assumes, rather, that these unknown factors have been neutralizedacross the treatment and control groups by randomization. This can be ahuge advantage over large-N cross-case methods, where each case must beassigned a specific score on all relevant control variables – often a highlyquestionable procedure, and one that must impose strong assumptions



about the shape of the underlying causal relationship (usually presumedto be linear).

Cross-Case TechniqueThe most useful statistical tool for identifying cases for in-depth anal-ysis in a most-similar setting is some variety of “matching” strategy.73

Statistical estimates of causal effects based on matching techniques havebeen a major topic in quantitative methodology over the last twenty-fiveyears, first in statistics74 and subsequently in econometrics75 and politicalscience.76

Matching techniques are based on an extension of experimental logic.In a randomized experiment, elaborate statistical models are unneces-sary for causal inference because, for a large enough selection of cases,the treatment group and the control group have a high probability ofbeing similar in their background characteristics (X2). Hence, a simpledifference-of-means test is often sufficient to analyze the effects of a treat-ment variable (X1) across groups.

In observational studies where the hypothesized causal factor (X1) isdichotomous, the situation is superficially the same. For purposes of dis-cussion, we shall refer to cases with a “high” score on X1 as members ofthe treatment group, and to cases with “low” scores as members of thecontrol group. Thus are observational studies translated into the lexiconof experimental analysis.

However, in observational studies it is unusual to find cases that differon X1 but not on various background characteristics (X2) that mightaffect the outcome of interest. For example, countries that are stronglydemocratic (or strongly authoritarian) are likely to be similar in morethan one respect. This greatly complicates the analysis of X1’s independenteffect on the outcome.

The traditional approach to this problem is to introduce a variablefor each potential confounder in a regression model of causal relation-ships. But this standard-issue technique requires a strong set of assump-tions about the behavior of the various factors introduced into the model.Matching techniques have been developed as an explicit alternative to

73 For good introductions, see Ho et al. (2004); Morgan and Harding (2005); Rosenbaum(2004); and Rosenbaum and Silber (2001). For a discussion of matching procedures inStata, see Abadie et al. (2001).

74 Rosenbaum and Rubin (1985); Rosenbaum (2004).75 Hahn (1998).76 Ho et al. (2004); Imai (2005).



the control-variable approach. This alternative begins by identifying a setof variables (other than the dependent variable or the main independentvariable) on which the cases are to be matched. Then, for each case inthe treatment group, the researcher identifies as many cases as possiblefrom the control group with the exact same scores on the matching vari-ables (the covariates). Finally, the researcher looks at the difference onthe dependent variable between the cases in the treatment group and thematching cases in the control group. If the set of matching variables isbroad enough to include all confounders, the average difference betweenthe treatment-group and the matching control-group cases should pro-vide a good estimate of the causal effect. Even in a situation in which theset of matching variables includes some, but not all, confounders, match-ing may produce better causal inferences than regression models becausecases that match on a set of explicitly selected variables are also morelikely to be similar on unmeasured confounders.77

Unfortunately, the relatively simple matching procedure just described,known as exact matching, is often impossible. This procedure typicallyfails for continuous variables such as wealth, age, and distance, since theremay be no two cases with the same score on a continuous variable. Forexample, there is no undemocratic country with the exact same per capitaGDP as the United States. Note that the larger the number of covariates,the lower the likelihood of finding exact matches.

In situations where exact matching is infeasible, researchers mayinstead employ approximate matching, where cases from the controlgroup that are close enough to matching cases from the treatment groupare accepted as matches. Major weaknesses of this approach include thefact that the definition of “close enough” is inevitably arbitrary, as wellas the fact that, for large sets of matching variables, few treatment casesare likely to have even approximate matches.

To deal with situations in which exact matching is impossible, method-ologists have developed an alternative procedure known as propensity-score matching. This approach suggests a somewhat different definition ofsimilarity than the previous two. Rather than focusing on sharing scoreson the matching variables, propensity-score matching focuses on sharinga similar estimated probability of having been in the treatment group,

77 However, matching is clearly inferior to a well-designed and well-executed randomizedexperiment. The benefits of matching extend only so far as equivalence on the variablesexplicitly included and any unmeasured variables that fortuitously happen to be similaracross the cases. By contrast, proper randomization handles all unmeasured variables.



conditional on the matching variables. In other words, when looking fora match for a specific case in the treatment group, researchers look forcases in the control group that – before the score on the independent vari-able is known – would have been as likely to be in the treatment groupas actually chosen cases. This is accomplished by a two-stage analysis,the first stage of which approaches the key independent variable, X1, as adependent variable and the matching variables as independent variables.(This is similar in spirit to selection models, where a two-stage approachto causal inference is adopted.) Once this model has been estimated, thecoefficient estimates are disregarded. Instead, the second stage of the anal-ysis employs the fitted values for each case, which tell us the probability ofthat case being assigned to the treatment group, conditional on its scoreson the matching variables. These fitted values are referred to as propen-sity scores. The final step in the process is to choose matches for each casein the treatment group. This is accomplished by selecting cases from thecontrol group with similar propensity scores.

The end result of this procedure is a set of matched cases that canbe compared in whatever way the researcher deems appropriate. Theseare the “most-similar” cases, returning to the qualitative terminology.Rosenbaum and Silber summarize the results of recent medical studies:

Unlike model-based adjustments, where patients vanish and are replaced by thecoefficients of a model, in matching, ostensibly comparable patterns are compareddirectly, one by one. Modern matching methods involve statistical modeling andcombinatorial algorithms, but the end result is a collection of pairs or sets ofpeople who look comparable, at least on average. In matching, people retaintheir integrity as people, so they can be examined and their stories can be toldindividually.78

Matching, conclude the authors, “facilitates, rather than inhibits, thickdescription.”79

Indeed, the same matching techniques that have been used successfullyin observational studies of medical treatments might also be adapted to thestudy of nation-states, political parties, cities, or indeed any paired casesin the social sciences. Suppose that, in order to study the relationshipbetween wealth and democracy, the researcher wishes to select a casethat is as similar as possible to Costa Rica in background variables, whilebeing as different as possible on per capita GDP, the variable of theoreticalinterest, and the outcome of interest, democracy.

78 Rosenbaum and Silber (2001: 223).79 Ibid.



In order to select most-similar cases for the study of the relationshipbetween wealth and democracy, one must arrive at a statistical model ofthe causes of a country’s wealth. Obviously, such a proposition is com-plex. Since this is an illustrative example, we shall be satisfied with acartoon model that includes only a few independent variables. A coun-try’s wealth will be assumed to be a function of the origin of its legalsystem (measured by dummy variables for English legal heritage, Frenchlegal heritage, socialist legal heritage, German legal heritage, and Scandi-navian legal heritage) and its geographic endowments (measured by thedistance of each country’s capital city from the equator).

The first step in selecting most-similar cases is to run a nonparametricregression with these independent variables and logged per capita GDP(the independent variable of theoretical interest) as the dependent vari-able. The fitted values from this regression serve as propensity scores,and cases with similar propensity scores are interpreted as matching. Thepropensity score for our focus case, Costa Rica, is 7.63. Examining thepropensity-score data, one sees that Benin has a propensity score of 7.58 –quite similar to Costa Rica’s. At the same time, Benin’s per capita GDPof $1,163 is substantially different from Costa Rica’s per capita GDP of$5,486, as are their democracy scores in 1995 (Benin is much less demo-cratic than Costa Rica). Hence, Costa Rica and Benin may be viewed asmost-similar cases for testing the relationship between wealth and democ-racy, as illustrated in Table 5.5. An in-depth analysis of these two casesmay shed light on the causal pathways between economic developmentand democracy. Indeed, these two cases are probably more informativethan other two-case comparisons precisely because the case-selection pro-cedure has identified countries whose other attributes are roughly equalin their propensity to democracy/authoritarianism. This means that thedifferences on the variable of theoretical interest (GDP per capita) and theoutcome (democracy) can be given a causal interpretation – an interpre-tation that would probably not be suggested by a qualitative assessmentof these two countries (which are quite different in culture, region, andhistorical experience).

It is important to keep in mind that the quality of the “match”depends entirely on the quality of the statistical model used to generatethe propensity scores. A superficial model like the one used here mayproduce rather superficial matches. Yet, in a large-N context – wheredozens, if not thousands of cases vie for inclusion – a formal approachto case selection offers significant advantages. At the very least, one’sassumptions are rendered transparent.



table 5.5. Paired cases resulting from matching procedure

GDP

per capita(X1)

Propensity score (X2)

Democracy

(Y)

Benin

Costa Rica

$1,163 7.58 6 Cases

$5,486 7.63 10

ConclusionThe most-similar method is one of the oldest recognized techniques ofqualitative analysis, harking back to J. S. Mill’s classic study, System ofLogic (first published in 1834). By contrast, matching statistics are a rela-tively new technique in the arsenal of the social sciences, and have rarelybeen employed for the purpose of selecting cases for in-depth analysis.Yet, as suggested in the foregoing discussion, there may be a fruitful inter-change between the two approaches. Indeed, the current popularity ofmatching among statisticians – relative, that is, to garden-variety regres-sion models – rests upon what qualitative researchers would recognize asa “case-based” approach to causal analysis. If Rosenbaum and Silber arecorrect, it may be perfectly reasonable to appropriate this large-N methodof analysis for case study purposes.

To be sure, the purpose of a case study is somewhat different in situa-tions where a large-N cross-case analysis has already been conducted.Here, the general causal relationship is usually clear. We know fromour cross-case study that GDP per capita is strongly associated withdemocracy; there is a strong presumption of causality. Of course, the casestudy analysis may give us reasons to doubt. Perhaps the causal path-ways from economic development to regime type are difficult to identify.Perhaps the presumed causal pathways, as identified by previous researchor theoretical hunch, are simply not in evidence. Even so, the usual pur-pose of a case study analysis in this setting is to corroborate an initialcross-case finding.

By contrast, if there is no prior cross-case investigation – at least noneof a formal nature – the case study performs a somewhat different role.Here, we will be more interested in the covariational patterns that arediscovered between X1 and Y. Thus, Epstein’s study of American andCanadian political parties is notable for its principal finding: that theunderlying cause of party cohesion is to be found in the structure of



the executive (parliamentary/presidential). Indeed, Epstein spends rela-tively little time in this article discussing possible causal mechanisms;his principal focus is on “scoring” the relevant variables, as discussed.By the same token, if Epstein had already conducted a large-N cross-case analysis prior to his case study, and if this cross-case analysis hadrevealed a strong pattern between executive type and party cohesion,his two-case analysis of the United States and Canada (cases that wepresume would have very similar propensity scores) would now serve arather different purpose. Evidently, the function of the most-similar casestudy shifts subtly but importantly when the case-selection procedure is,itself, a mode of analysis, offering strong prima facie evidence of a causalrelationship.

As with other methods of case selection, the most-similar method isprone to problems of non-representativeness. If this technique is employedin a qualitative fashion (without a systematic cross-case selection strat-egy), potential biases in the chosen cases must be addressed in a spec-ulative way. If the researcher employs a matching technique of caseselection within a large-N sample, the problem of potential bias can beaddressed by assuring a choice of cases that are not extreme outliers, asjudged by their residuals in the full model. Most-similar cases should alsobe “typical” cases, though some scope for deviance around the regres-sion line may be acceptable for purposes of finding a good fit amongcases.

Most-Different Cases

A final case-selection method is the reverse image of the previous method.Here, variation on independent variables is prized, while variation on theoutcome is eschewed. Rather than looking for cases that are most-similar,one looks for cases that are most-different. Specifically, the researcher triesto identify cases where just one independent variable (X1), as well as thedependent variable (Y), covary, while all other plausible factors (X2a−d)show different values.80

80 The most-different method is sometimes referred to as the “method of agreement,” fol-lowing its inventor, J. S. Mill (1843/1872). See also DeFelice (1986); Gerring (2001:212–14); Lijphart (1971, 1975); Meckstroth (1975); Przeworski and Teune (1970);and Skocpol and Somers (1980). For examples of this method, see Collier and Col-lier (1991/2002); Converse and Dupeux (1962); Karl (1997); Moore (1966); Skocpol(1979); and Yashar (2005: 23). However, most of these studies are described as combin-ing most-similar and most-different methods.



table 5.6. Most-different analysis with two cases

X1 X2a X2b X2c X2d Y

A 1 1 0 1 0 1 Casetypes B 1 0 1 0 1 1

X1 = the variable of theoretical interest. X2a−d = a vectorof controls. Y = the outcome of interest.

The simplest form of this two-case comparison is illustrated in Table5.6. Cases A and B are deemed “most-different,” though they are similarin two essential respects – the causal variable of interest and the outcome.

As an example, I follow Marc Howard’s recent work, which exploresthe enduring impact of communism on civil society.81 Cross-national sur-veys show a strong correlation between former communist regimes andlow social capital, controlling for a variety of possible confounders. It is astrong result. Howard wonders why this relationship is so strong and whyit persists, and perhaps even strengthens, in countries that are no longersocialist or authoritarian. In order to answer this question, he focuses ontwo most-different cases, Russia and East Germany. These two countrieswere quite different – in all ways other than their communist experience –prior to the Soviet era, during the Soviet era, and in the post-Soviet era,as East Germany was absorbed into West Germany. Yet they both scorenear the bottom of various cross-national indices intended to measure theprevalence of civic engagement in the current era. Thus, Howard’s caseselection procedure meets the requirements of the most-different researchdesign: variance is found on all (or most) dimensions aside from the keyfactor of interest (communism) and the outcome (civic engagement).82

What leverage is brought to the analysis by this approach? Howard’scase studies combine evidence drawn from mass surveys and from in-depth interviews of small, stratified samples of Russians and East Ger-mans. (This is a good illustration, incidentally, of how quantitative andqualitative evidence can be fruitfully combined in the intensive study ofseveral cases.) The product of this analysis is the identification of threecausal pathways that, Howard claims, help to explain the laggard statusof civil society in post-communist polities: “the mistrust of communist

81 Howard (2003). In the following discussion I treat the terms “social capital,” “civilsociety,” and “civic engagement” interchangeably.

82 Howard (2003: 6–9).



organizations, the persistence of friendship networks, and the disappoint-ment with post-communism.”83 Simply put, Howard concludes, “a greatnumber of citizens in Russia and Eastern Germany feel a strong and lin-gering sense of distrust of any kind of public organization, a general sat-isfaction with their own personal networks (accompanied by a sense ofdeteriorating relations within society overall), and disappointment in thedevelopments of post-communism.”84

Results obtained from the analysis of East Germany and Russia are pre-sumed to apply in other post-communist polities (e.g., Lithuania, Poland,Bulgaria, Albania). Indeed, by choosing a heterogenous sample, Howardsolves potential problems of representativeness in his restricted sample.However, this sample is not representative across the entire population ofthe inference, which is intended to cover all countries, not just commu-nist ones. (To argue that communism impedes the development of civilsociety is to imply that noncommunism stimulates the development ofcivil society. The chosen sample is truncated [censored] on the dependentvariable).

Equally problematic is the lack of variation on key causal factors ofinterest – communism and its putative causal pathways. For this reason, itis generally difficult to reach conclusions about the causal status of thesefactors on the basis of the most-different analysis alone. It is possible,that is, that the three causal pathways identified by Howard also operatewithin polities that have never experienced communist rule. If so, theyare not properly regarded as causal.

Nor does it seem possible to conclusively eliminate rival hypotheseson the basis of this most-different analysis. Indeed, this is not Howard’sintention. He wishes merely to show that whatever influence on civil soci-ety might be attributed to economic, cultural, and other factors does notexhaust this subject.

My considered judgment, based on the foregoing methodologicaldilemmas, is that the most-different research design provides only minimalinsight into the problem of why communist systems appear to suppresscivic engagement, years after their disappearance. Fortunately, this is notthe only research design employed by Howard in his admirable study.Indeed, the author employs two other small-N cross-case methods, aswell as a large-N cross-country statistical analysis. In my opinion, thesemethods do most of the analytic work. East Germany may be regarded

83 Ibid., 122.84 Ibid., 145.



as a causal-pathway case (as discussed earlier). It has all the attributesnormally assumed to foster civic engagement (e.g., a growing economy,multiparty competition, civil liberties, a free press, close association withWestern European culture and politics), but nonetheless shows little or noimprovement on this dimension during the post-transition era.85 It is plau-sible to attribute this lack of change to its communist past, as Howarddoes. The contrast between East and West Germany provides a most-similar analysis, since the two polities share virtually everything excepta communist past. This variation is also deftly exploited by Howard. Inshort, Howard’s conclusions are justifiable, but not on the basis of most-different analysis.

I do not wish to dismiss the most-different research method entirely.Surely, Howard’s findings are stronger with the intensive analysis of Russiathan they would be without. Yet if one strips away the pathway case (EastGermany) and the most-similar analysis (East/West Germany), there islittle left upon which to base an analysis of causal relations (aside fromthe large-N cross-national analysis). Indeed, most scholars who employthe most-different method do so in conjunction with other methods.86 Itis rarely, if ever, a stand-alone method.87

ConclusionGeneralizing from this discussion of Marc Howard’s work, I offer the fol-lowing summary remarks on the most-different method of case analysis.(I leave aside issues faced by all case study analyses, issues that formedthe basis of Chapter Three.)

85 Ibid., 8.86 See, e.g., Collier and Collier (1991/2002); Karl (1997); Moore (1966); Skocpol (1979);

and Yashar (2005: 23). Karl (1997), which affects to be a most-different system analysis(20), is a particularly clear example of this. Her study, focused ostensibly on petro-states (states with large oil reserves), makes two sorts of inferences. The first concernsthe (usually) obstructive role of oil in political and economic development. The secondsort of inference concerns variation within the population of petro-states, showing thatsome countries (e.g., Norway, Indonesia) manage to avoid the pathologies brought onelsewhere by oil resources. When attempting to explain the constraining role of oil onpetro-states, Karl usually relies on contrasts between petro-states and non-petro-states(e.g., Chapter 10). Only when attempting to explain differences among petro-states doesshe restrict her sample to petro-states. In my opinion, very little use is made of the most-different research design.

87 This was recognized, at least implicitly, by Mill (1843/1872: 258–9). Skepticism has beenechoed by methodologists in the intervening years (e.g., Cohen and Nagel 1934: 251–6;Gerring 2001; Skocpol and Somers 1980). Indeed, explicit defenses of the most-differentmethod are rare (but see DeFelice 1986).



Let us begin with a methodological obstacle that is faced by both Mil-lean styles of analysis – the necessity of dichotomizing every variable inthe analysis. Recall that, as with most-similar analysis, differences acrosscases must be sizeable enough to be interpretable in an essentially dichoto-mous fashion (e.g., high/low, present/absent), and similarities must beclose enough to be understood as essentially identical (e.g., high/high,present/present). Otherwise the results of a Millean-style analysis are notinterpretable. The problem of “degrees” is deadly if the variables underconsideration are by nature continuous (e.g., GDP). This is a particu-lar concern in Howard’s analysis, where East Germany scores somewhathigher than Russia in civic engagement; they are both low, though Russiais considerably lower. Howard assumes that this divergence is minimalenough to be understood as a difference of degree rather than of kind,a judgment that might be questioned. In these respects, most-differentanalysis is no more secure – but also no less – than most-similar analysis.

In one respect, most-different analysis is superior to most-similar anal-ysis. If the coding assumptions are sound, the most-different researchdesign may be useful for eliminating necessary causes. Causal factors thatdo not appear across the chosen cases – e.g., X2a−d in Table 5.6 – are evi-dently unnecessary for the production of Y. However, it does not followthat the most-different method is the best method for eliminating neces-sary causes. Note that the defining feature of this method is the sharedelement across cases – X1 in Table 5.6. This feature does not help one toeliminate necessary causes. Indeed, if one were focused solely on eliminat-ing necessary causes, one would presumably seek out cases that registerthe same outcomes and have maximum diversity on other attributes. InTable 5.6, this would be a set of cases that satisfy conditions X2a−d, butnot X1. Thus, even the presumed strength of the most-different analysisis not so strong.

Usually, case study analysis is focused on the identification (or clarifi-cation) of causal relations, not on the elimination of possible causes. Inthis setting, the most-different technique is useful, but only if assump-tions of “causal uniqueness” hold. By this I mean a situation in which agiven outcome is the product of only one cause: Y cannot occur except inthe presence of X1. X1 is necessary, and in some situations (given certainbackground conditions) sufficient, to cause Y.88

Consider the following hypothetical example. Suppose that a new dis-ease, about which little is known, has appeared in Country A. There are

88 Another way of stating this is to say that X is a “nontrivial necessary condition” of Y.



hundreds of infected persons across dozens of affected communities inthat country. In Country B, located at the other end of the world, severalnew cases of the disease surface in a single community. In this setting,we can imagine two sorts of Millean analyses. The first examines twosimilar communities within Country A, one of which has developed thedisease and the other of which has not. This is the most-similar style ofcase comparison, and focuses accordingly on the identification of a dif-ference between the two cases that might account for variation across thesample. A second approach focuses on (highly dissimilar) communitieswhere the disease has appeared across the two countries and searches forany similarities that might account for these similar outcomes. This is themost-different research design.

Both are plausible approaches to this particular problem, and we canimagine epidemiologists employing them simultaneously. However, themost-different design demands stronger assumptions about the underly-ing factors at work. It supposes that the disease arises from the same causein any setting. This may be a reasonable operating assumption when oneis dealing with certain natural phenomena like diseases. Even so, there aremany exceptions. Death, for example, has many causes. For this reason,it would not occur to us to look for most-different cases of high mortalityaround the world. In order for the most-different research design to effec-tively identify a causal factor at work in a given outcome, the researchermust assume that X1 – the factor held constant across the diverse cases –is the only possible cause of Y (see Table 5.6). This assumption rarelyholds in social scientific settings, for most outcomes of interest to anthro-pologists, economists, political scientists, and sociologists have multiplecauses. There are many ways to win an election, to build a welfare state,to get into a war, to overthrow a government, or – returning to MarcHoward’s work – to build a strong civil society. And it is for this reasonthat most-different analysis is rarely applied in social science work and,where applied, is rarely convincing.

If this seems a tad severe, there is a more charitable way of approachingthe most-different method. Arguably, this is not a pure “method” at all butmerely a supplement, a way of incorporating diversity in the subsample ofcases that provide the unusual outcome of interest. If the unusual outcomeis revolution, one might wish to encompass a wide variety of revolutionsin one’s analysis. If the unusual outcome is post-communist civil society,it seems appropriate to include a diverse set of post-communist polities inone’s sample of case studies, as Marc Howard does. From this perspective,the most-different method (so-called) might be better labeled a diverse-case method, as explored earlier.



Conclusion

In order to be a case of something broader than itself, the chosen case mustbe representative (in some respects) of a larger population. Otherwise – ifit is purely idiosyncratic (“unique”) – it is uninformative about anythingother than itself. A study based on a nonrepresentative sample has no(or very little) external validity. To be sure, no phenomenon is purelyidiosyncratic; the notion of a unique case is a matter that would be difficultto define. One is concerned, as always, with matters of degree. Cases aremore or less representative of some broader phenomenon and, on thatscore, may be considered better or worse subjects for intensive analysis.(The one exception, as noted, is the influential case.)

Of all the problems besetting case study analysis, perhaps the most per-sistent – and the most persistently bemoaned – is the problem of samplebias.89 Lisa Martin finds that the overemphasis of international relationsscholars on a few well-known cases of economic sanctions – most of whichfailed to elicit any change in the sanctioned country – “has distorted ana-lysts’ view of the dynamics and characteristics of economic sanctions.”90

Barbara Geddes charges that many analyses of industrial policy havefocused exclusively on the most successful cases – primarily the East AsianNICs – leading to biased inferences.91 Anna Breman and Carolyn Sheltonshow that case study work on the question of structural adjustment is sys-tematically biased insofar as researchers tend to focus on disaster cases –those where structural adjustment is associated with very poor health andhuman development outcomes. These cases, often located in sub-SaharanAfrica, are by no means representative of the entire population. Conse-quently, scholarship on the question of structural adjustment is highlyskewed in a particular ideological direction (against neoliberalism).92

89 Achen and Snidal (1989); Collier and Mahoney (1996); Geddes (1990); King, Keohaneand Verba (1994); Rohlfing (2004); Sekhon (2004). Some case study researchers appearto denigrate the importance of case representativeness. George and Bennett (2005: 30)write emphatically, “Case researchers do not aspire to select cases that are directly ‘rep-resentative’ of diverse populations and they usually do not and should not make claimsthat their findings are applicable to such populations except in contingent ways.” How-ever, it becomes clear that what the authors are inveighing against is not the goal ofrepresentativeness per se but rather the problem of a case study researcher who claimsan inappropriately broad extension for her findings. “To the extent that there is a rep-resentativeness problem or a selection bias problem in a particular case study, it is oftenbetter described as the problem of ‘overgeneralizing’ findings to types or subclasses ofcases unlike those actually studied” (ibid., 32).

90 Martin (1992: 5).91 Geddes (1990).92 Breman and Shelton (2001). See also Gerring, Thacker, and Moreno (2005).



These examples might be multiplied many times. Indeed, for many top-ics the most-studied cases are acknowledged to be less than representa-tive. It is worth reflecting upon the fact that our knowledge of the worldis heavily colored by a few “big” (populous, rich, powerful) countries,and that a good portion of the disciplines of economics, political science,and sociology are built upon scholars’ familiarity with the economics,political science, and sociology of one country, the United States.93 Casestudy work is particularly prone to problems of investigator bias becauseso much rides on the researcher’s selection of one case (or a few cases).Even if the investigator is unbiased, her sample may still be biased simplyby virtue of “random” error (which may be understood as measurementerror, error in the data-generation process, or an underlying causal featureof the universe).

There are only two situations in which a case study researcher neednot be concerned with the representativeness of her chosen case. The firstis the influential-case research design, where a case is chosen because ofits possible influence on a cross-case model, and hence is not expectedto be representative of a larger sample. The second is the deviant-casemethod, where the chosen case is employed to confirm a broader cross-case argument to which the case stands as an apparent exception. Yet inthe latter instance, the chosen case is expected to be representative of abroader set of cases – those, in particular, that are poorly explained bythe extant model.

In all other circumstances, cases must be representative of the popula-tion of interest in whatever ways might be relevant to the propositionin question. Note that where a researcher is attempting to disconfirm adeterministic proposition, the question of representativeness is perhapsmore appropriately understood as a question of classification: is thechosen case appropriately classified as a member of the designatedpopulation? If so, then it is fodder for a disconfirming case study.

If the researcher is attempting to confirm a deterministic proposition,or to make probabilistic arguments about a causal relationship, then theproblem of representativeness is of the more usual sort: is Case A unit-homogenous relative to other cases in the population? This is not aneasy matter to test. However, in a large-N context the residual for that

93 Wahlke (1979: 13) writes of the failings of the “behavioralist” mode of political scienceanalysis. “It rarely aims at generalization; research efforts have been confined essentiallyto case studies of single political systems, most of them dealing . . . with the Americansystem.”



case (in whatever model the researcher has greatest confidence in) is areasonable place to start. Of course, this test is only as good as the modelat hand. Any incorrect specifications or incorrect modeling procedureswill likely bias the results and give an incorrect assessment of each case’s“typicality.” In addition, there is the possibility of stochastic error, errorsthat cannot be modeled in a general framework. Given the explanatoryweight that individual cases are asked to bear in a case study analysis, itis wise to consider more than just the residual test of representativeness.Deductive logic and an in-depth knowledge of the case in question areoften more reliable tools than the results of a rather superficial cross-casemodel.

In any case, there is no dispensing with the question. Case studies (withthe two exceptions already noted) rest upon an assumed synecdoche: thecase should stand for a population. If this is not true, or if there is reasonto doubt this assumption, then the utility of the case study is broughtseverely into question.

Fortunately, there is some safety in numbers. Insofar as case study evi-dence is combined with cross-case evidence, the issue of sample bias ismitigated. Indeed, the skepticism about case study work that one com-monly encounters in the social sciences today is, in my view, a productof a too-literal interpretation of the case study method. A case study toutcourt is thought to mean a case study tout seul. Insofar as case studiesand cross-case studies can be enlisted within the same investigation (eitherin the same study or by reference to other studies of the same subject),problems of representativeness are less worrisome. This is the virtue ofcross-level work, a.k.a. “triangulation.”

AmbiguitiesBefore concluding, I wish to draw attention to two ambiguities in case-selection strategies for case study research. The first concerns the admix-ture of several case-selection strategies. The second concerns the changingstatus of a case as a study proceeds.

Some case studies follow only one strategy of case selection. Theyare typical, diverse, extreme, deviant, influential, crucial, pathway, most-similar, or most-different research designs, as discussed. However, manycase studies mix and match among these case-selection strategies. Indeed,insofar as all case studies seek representative samples, they are all in searchof “typical” cases. Thus, it is common for writers to declare that their caseis, for example, both extreme and typical; it has an extreme value on X1

or Y but is not, in other respects, idiosyncratic. There is not much that



one can say about these combinations of strategies except that, wherethe cases allow for a variety of empirical strategies, there is no reasonnot to pursue them. And where the same case legitimately serves severalfunctions at once (without further effort on the researcher’s part), thereis little cost to a multipronged approach to case analysis.

The second issue that deserves emphasis is the changing status of a caseduring the course of a researcher’s investigation – which may last for years,if not decades. The problem is particularly acute when a researcher beginsin an exploratory mode and then proceeds to hypothesis testing (that is,she develops a specific X1/Y proposition), or when the operative hypoth-esis or key control variable changes (a new causal factor is discovered oranother outcome becomes the focus of analysis). Things change. And it isthe mark of a good researcher to keep her mind open to new evidence andnew insights. Too often, methodological discussions give the misleadingimpression that hypotheses are clear and remain fixed over the courseof a study’s development. Nothing could be further from the truth. Theunofficial transcripts of academia – accessible in informal settings, whereresearchers let their guards down (particularly if inebriated) – are filledwith stories about dead ends, unexpected findings, and drastically revisedtheory chapters. It would be interesting, in this vein, to compare publishedwork with dissertation prospectuses and fellowship applications. I doubtthat the correlation between these two stages of research is particularlystrong.

Research, after all, is about discovery, not simply the verification or fal-sification of existing hypotheses. That said, it is also true that research ona particular topic should move from hypothesis generating to hypothesistesting. This marks the progress of a field, and of a scholar’s own work.As a rule, research that begins with an open-ended (X- or Y-centered)analysis should conclude with a determinate X1/Y hypothesis.

The problem is that research strategies that are ideal for explorationare not always ideal for confirmation. I discussed this trade-off in ChapterThree as it pertains to the cross-case/case study dilemma. It also appliesto various methods of case study analysis, as presented in this chapter.The extreme-case method is inherently exploratory, since there is no clearcausal hypothesis; the researcher is concerned merely to explore varia-tion on a single dimension (X1 or Y). Other methods can be employedin either an open-ended (exploratory) or a hypothesis-testing (confirma-tory/disconfirmatory) mode. The difficulty is that once the researcher hasarrived at a determinate hypothesis, the originally chosen research designmay no longer be so well constructed.



This is unfortunate, but inevitable. One cannot construct the perfectresearch design until (a) one has a specific hypothesis and (b) one is rea-sonably certain about what one is going to find “out there” in the empir-ical world. This is particularly true of observational research designs, butit also applies to many experimental research designs: usually, there isa “good” (informative) finding, and a finding that is less insightful. Inshort, the perfect case study research design is usually apparent only expost facto.

There are three ways to handle this. One can explain, straightforwardly,that the initial research was undertaken in an exploratory fashion, andtherefore not constructed to test the specific hypothesis that is – now – theprimary argument. Alternatively, one can try to redesign the study afterthe new (or revised) hypothesis has been formulated. This may requireadditional field research or perhaps the integration of additional cases orvariables that can be obtained through secondary sources or consultationof experts. A final approach is to simply jettison, or deemphasize, thatportion of the research that no longer addresses the (revised) key hypoth-esis. A three-case study may become a two-case study, and so forth. Losttime and effort are the costs of this downsizing.

In the event, practical considerations will probably determine whichof these three strategies, or combinations of strategies, is to be followed.The point to remember is that revision of one’s cross-case research designis normal and to be expected. Not all twists and turns on the meanderingtrail of truth can be anticipated.

Are There Other Methods of Case Selection?At the outset of this chapter, I summarized the task of case selection asa matter of achieving two objectives: representativeness (typicality) andvariation (causal leverage). Evidently, there are other objectives as well.For example, one wishes to identify cases that are independent of eachother. If chosen cases are affected by each other, the problem (sometimesknown as Galton’s problem or a problem of diffusion) must be correctedbefore analysis can take place. I have neglected this issue because it isusually apparent to the researcher and, in any case, there are no easytechniques that might be utilized to correct for such biases.94

I have also disregarded pragmatic/logistical issues that might affect caseselection. Evidently, case selection is often influenced by a researcher’s

94 For further discussion of this and other factors impinging upon case selection, see Gerring(2001: 178–81).



familiarity with the language of a country, a personal entree into thatlocale, special access to important data, or funding that covers one archiverather than another. Pragmatic considerations are often – and quiterightly – decisive in the case-selection process.

A final consideration concerns the theoretical prominence of a partic-ular case within the literature on a subject. Researchers are sometimesobliged to study cases that have received extensive attention in previ-ous studies. These are sometimes referred to as “paradigmatic” cases or“exemplars.”95

However, neither pragmatic/logistical utility nor theoretical promi-nence qualifies as a methodological factor in case selection. That is, thesefeatures of a case have no bearing on the validity of the findings stemmingfrom a study. As such, it is appropriate to grant these issues a peripheralstatus in this chapter, as I have elsewhere in the book.

One final caveat must be issued. While it is traditional to make a dis-tinction between the tasks of case selection and case analysis, a close lookat these processes reveals them to be indistinct and overlapping. One can-not choose a case without considering the sort of analysis that it might besubjected to, and vice versa. Thus, the reader should consider choosingcases by employing the nine techniques laid out in this chapter along withany considerations that might be introduced by virtue of a case’s quasi-experimental qualities (Chapter Six) and its potential for process tracing(Chapter Seven), subjects to which we now turn.

95 Flyvbjerg (2004: 427).


6

Internal Validity

An Experimental Template

Let us suppose that one has chosen one’s case (or cases) according toone of the techniques (or some combination of techniques) described inthe previous chapter. And let us further suppose that one has refinedone’s research question into a specific (X1/Y) hypothesis. One then facesa problem of internal validity. How does one construct a research designthat might illuminate the causal relationship of interest?

The fundamental problem of causal inference is that one cannot rerunhistory to see what effects X1 actually had on Y in a particular case. At anontological level, this problem is unsolvable. There are no time machines.However, there are various ways of reducing uncertainty so that causalinference is possible, and indeed quite plausible. The argument of thischapter is that the various methods of doing so are all quasi-experimentalin nature. This is because the true experiment is the closest approximationwe have at our disposal to a time machine. Through this technique, andothers modeled on it, one can imagine what it would be like to go backin time, alter a “treatment,” and observe its true causal effect.

This chapter thus calls into question some of the usual assumptionsapplied to case study research. Most case study researchers perceive onlya distant and tenuous connection between their work and the laboratoryexperiment, with a manipulated treatment and randomized control. Theyare inclined to the view that experimental and observational work inhabitdifferent worlds, perhaps even employ different logics of inquiry. Granted,case study researchers working with observational data occasionally referto their work as “quasi-experiments,” “natural experiments,” “thoughtexperiments,” “crucial experiments,” or “counterfactual thought exper-iments.” However, these designations are often loose and ambiguous.

151



Arguably, they obscure more than they clarify. What does it mean for acase study to be quasi-experimental, and how might case study researchbe reconstructed through the lens of the experimental method?

I believe that, in those instances where case study research is warranted,the strongest methodological defense for this research design often derivesfrom its quasi-experimental qualities. All case study research is quasi-experimental. But some case studies are more experimental than others.

An Experimental Template

Broadly speaking, there are two dimensions upon which any causal effectmay be observed – temporal and spatial. Temporal effects may be observeddirectly when an intervention occurs: X1 intervenes upon Y, and weobserve any change in Y that may follow. Here, the “control” is the pre-intervention state of Y; what Y was prior to the intervention (a statethat we presume would remain the same, or whose trend would remainconstant, in the absence of intervention). Spatial effects may be observeddirectly when two phenomena are similar enough to be understood asexamples (cases) of the same thing. Ideally, they are similar in all respectsbut one – the causal factor of interest. In this situation, the “control” isthe case without the intervention.

Classic experimental research designs achieve variation through timeand across space, thus maximizing leverage into the fundamental problemof causal inference. Here, we apply the same dimensions to all research,whether or not the treatment is manipulated. This produces a matrix withfour cells, as illustrated in Figure 6.1. Cell 1, understood as a DynamicComparison, mirrors the paradigmatic laboratory experiment, since itexploits temporal and spatial variation. Cell 2, labeled a LongitudinalComparison, employs only temporal variation and is similar in designto an experiment without control. Cell 3, dubbed a Spatial Comparison,employs only spatial variation; it purports to measure the outcome ofan intervention that occurred at some point in the past but is not directlyobservable. Cell 4, a Counterfactual Comparison, relies on variation (tem-poral and/or spatial) that is imaginary, that is, where the researcher seeksto replicate the circumstances of an experiment in her head or with theaid of some mathematical (perhaps computer-generated) model.1

1 One always hesitates to introduce new terms to an already confusing semantic field.However, there are good reasons to shy away from the traditional lexicon. To begin with,most of the terms associated with case study research have nothing to do with the empirical


Internal Validity: An Experimental Template 153

Spatial variation:

Yes No

Yes1. Dynamic

comparison2.Longitudinal

comparisonTemporalvariation:

No3. Spatial

comparison4. Counterfactual

comparison

figure 6.1. Matrix of case study research designs.

In order to familiarize ourselves with the differences among these fourparadigmatic research designs, it may be useful to begin with a series ofscenarios built around a central (hypothetical) research question: doesthe change from a first-past-the-post (FPP) electoral system to a list-proportional (list-PR) electoral system moderate interethnic attitudinalhostility in a polity with high levels of ethnic conflict? Let us assume thatone can effectively measure interethnic hostility through a series of pollsadministered to a random sample (or panel) of respondents at regularintervals throughout the research period. This registers the outcome ofthe study, the propensity for people to hold hostile attitudes toward otherethnic groups.2 With this setup, how might one apply the four foregoingdesigns?

A Dynamic Comparison would proceed by the selection of two commu-nities that are similar in all respects, including the employment of a majori-tarian electoral system and relatively high levels of interethnic hostility.The researcher would then either administer an electoral system change,

variation embodied in the case chosen for intensive analysis. As such, they focus attentionon how a case is situated within a broader population of cases (e.g., “extreme,” “deviant,”“typical,” “nested”) or on the perceived function of that case within some field of study(e.g., “exploratory,” “heuristic,” “confirmatory”). These issues, while important, do notspeak to the causal leverage that might be provided by a chosen case(s). Mill’s suggestionof a “most-similar” research design (a.k.a. the Method of Difference) is directly relevantto the covariational properties of chosen cases. However, it is strikingly ambiguous, sinceit may refer to a set of cases where there is an intervention (a change on the key variableof theoretical interest) or where there is no intervention. These are quite different kindsof comparisons, as signaled by the typology (the first is much more informative than thesecond), and deserve to be called by different names. Thus, in the interests of clarity, anew set of categories is amply justified.

2 I recognize that the attitudes do not directly link to behavior, and thus measuring attitu-dinal hostility will not directly translate into the manifestation of interethnic behavioralhostility.



or hope for a naturally occurring electoral system reform in one of thesecommunities, holding the other constant. The final step would be to com-pare the results to see if there is a difference over time between treatmentand control groups.

A Longitudinal Comparison would follow the same procedure, butwithout the control group. Consequently, the researcher’s judgment ofresults rests solely on a before/after comparison of interethnic conflict inthe community that undergoes a change in its electoral system.

A Spatial Comparison is identical to the Dynamic Comparison exceptthat in this instance there is no observable intervention. Here, theresearcher again searches for two communities similar in various respectsthat might affect interethnic hostility. One happens to employ a majori-tarian electoral system, while the other has a proportional electoral sys-tem. This spatial variation on the key independent variable forms thecrux of causal inference, but is not observable through time. The researchquestion, based upon a survey of attitudes in the two communities, iswhether interethnic hostility is lower in the community using PR electoralrules.

In a Counterfactual Comparison, finally, the researcher observes a com-munity with a majoritarian electoral system and high levels of interethnichostility that does not undergo an electoral system change to PR. Sincethere is no observable change over time in the key variable of interest, heronly leverage on this question is the counterfactual: what would have hap-pened, in all likelihood, if this country had reformed its electoral system?

The essential properties of these four research designs are illustrated inTable 6.1, where Y refers to the outcome of concern, X1 marks the inde-pendent variable of interest, and X2 represents a vector of controls (otherexogenous factors that might influence the outcome). These controls maybe directly measured or simply assumed (as they often are in randomizedexperiments). The initial value of X1 is denoted as “−” and a change ofstatus as “+.” The vector of controls, by definition, remains constant. Aquestion mark indicates that the value of the dependent variable is themajor objective of the analysis. Observations are taken before (t1) andafter (t2) an intervention and thus comprise pre- and post-tests.

In these examples, an intervention (a change in X1) may be manipulatedor natural, sudden or slow, major or minuscule, dichotomous or continu-ous, and causal effects may be immediate or lagged. For ease of discussion,I shall speak of interventions as dichotomous (present/absent, high/low,on/off), but the reader should keep in mind that the actual researchsituation may be more variegated (though this inevitably complicates the



table 6.1. An experimental template for case study research designs

EXAMPLE

Hypothesis: A change from FPP to list-PR mitigates ethnic hostility.t1 t2

Y - | ?Treatment X1 - | +

X2 - | -Y - ?

Control X1 - -

1. Dynamic Comparison

X2 - -

Two similar communities with FPP electoral systems and high ethnichostility, one of which changes from FPP to list-PR. Ethnic hostility iscompared in both communities before and after the intervention.

t1 t2

Y - | ?X1 - | +

2. Longitudinal Comparison

Treatment

X2 - | -

A community with an FPP electoral system and high ethnic hostilitychanges to list-PR. Ethnic hostility is compared before and after theintervention.

t1

Y ?Treatment X1 +

X2 -Y ?

Control X1 -

3. Spatial Comparison

X2 -

Two similar communities, one of which has FPP and the other list-PR.Ethnic hostility is compared in both communities.

t1 [t2]Y - | ?

Treatment X1 - | +4. Counterfactual Comparison

X2 - | -

A community with an FPP electoral system and high ethnic hostility isconsidered, by a counterfactual thought experiment, to undergo a change tolist-PR. (t2 is hypothetical.)

Cases: Observations:Treatment = with intervention t1 = pre-test (before intervention)Control = without intervention t2 = post-test (after intervention)

Variables: Cells:Y = outcome | = interventionX1 = independent variable of interest − = stasis (no change in status of variable)X2 = a vector of controls + = change (variable changes value or trend

alters)? = the main empirical finding: Y changes

(+) or does not (−)

interpretation of a causal effect). Thus, I use the term intervention (a.k.a.“event” or “stimulus”) in the broadest possible sense, indicating any sortof change in trend in the key independent variable, X1. It should be under-lined that the absence of an intervention does not mean that a case doesnot change over time; it means simply that it does not experience a changeof trend. Any evaluation of an intervention involves an estimate of thebaseline – what value a case would have had without the intervention. A“+” therefore indicates a change in this baseline trend.

A key point, and one liable to misunderstanding, is that an interven-tion (a change in X1) refers to a change in the independent variable oftheoretical interest, not to changes in other variables. By contrast, an



“exogenous shock” research design, as that term is sometimes employed,is one where a peripheral variable intervenes upon a set of cases and theresearcher observes the results across some set of outcomes. For exam-ple, Robert Putnam’s study of social capital in Italy makes use of the factthat the country experienced a far-reaching decentralization of power in1970.3 Consequently, it was possible to observe institutional divergenceacross regions during the subsequent period; regions became a viable unitof analysis. Italy’s constitutional reform thus serves the function of anexogenous shock because it is unaffected by any of the factors Putnamwishes to study. However, the shock is not quasi-experimental, in thesense in which we have been using the term, precisely because the inter-vention is unrelated to the causal factor of theoretical interest. For anintervention to be experimental, it must embody the treatment of theoret-ical interest. In this instance, an experimental treatment would presum-ably involve a change in levels of social capital (it is not clear how thistreatment would be administered), thus allowing for pre- and post-teststhat would measure the causal impact of the intervention. Thus, Putnam’sstudy, as constructed, is properly classified as a Spatial Comparison amongregions.

Because interventions may be multiple or continuous within a singlecase, it follows that the number of temporal observations within a givencase may also be extended indefinitely. This might involve a very longperiod of time (e.g., centuries) or multiple observations taken over a shortperiod of time (e.g., an hour). Observations are thus understood to occurtemporally within each case (t1, t2, t3, . . . tn).

Although the number of cases in the following examples varies, and issometimes limited to one or two, research designs may – in principle –incorporate any number of cases. Thus, the designations “treatment” and“control” in Table 6.1 may be understood to refer to individual cases orto groups of cases. (In this chapter, “case” and “group” are used inter-changeably.) The caveat is that, at a certain point, it is no longer possibleto conduct an in-depth analysis of a case (because there are so many), andthus the research loses its case study designation.

In numbering these research designs (1–4), I intend to indicate a gradualfalling away from the experimental ideal. However, it would be incorrectto assume that a higher number necessarily indicates an inferior researchdesign. To begin with, my discussion in this chapter focuses on issues of

3 Putnam et al. (1993). For other examples of exogenous-shock research designs, see Mac-Intyre (2003) and Lieberman (2005b).



internal validity. Sometimes the need for greater external validity promptsa research design that is less “experimental.” Equally important is theubiquitous ceteris paribus assumption – that all peripheral factors thatmight affect the X1/Y relationship of interest are held constant, beforeand after the intervention and/or across treatment and control groups.Usually, ceteris paribus assumptions are more secure in experimental con-texts, but not always. This issue is taken up in the final section of thechapter.

Dynamic Comparison

The classic experiment involves one or more cases observed through timewhere the key independent variable undergoes a manipulated change. Oneor more additional cases (the control group), usually chosen randomly,are not subject to treatment. Consequently, the analyst observes bothtemporal and spatial variation.

Experimental research designs have long served as the staple methodof psychology and are increasingly common in other social sciences.4

For practical reasons, experiments are usually easiest to conduct wherethe units of analysis are comprised of individuals or small groups. Thus,experimental work in political science most commonly concerns the expla-nation of vote choice, political attitudes, party identification, and othertopics grouped together under the rubric of “political behavior.” An anal-ogous subfield has developed in economics, where it is known as “behav-ioral (or experimental) economics.”

Experiments may be conducted in laboratory settings or in naturalsettings. One innovative natural-setting approach employs a standardmass survey with a split-question format.5 Randomly chosen respondentsare divided into several groups (which may be denoted as “treatment”or “control” groups), each of which is administered a slightly differentsurvey. Since the intervention (the setup, the question, or the questionordering) is different, the results are interpretable in the same way thatalterations might be in the case of a laboratory intervention.

4 Admonitions to social scientists to adopt experimental methods can be found in Mill(1843/1872), and much later in Fisher (1935); Gosnell (1926); and Stouffer (1950). Forgeneral discussion, see Achen (1986); Campbell (1988); Campbell and Stanley (1963);Kagel and Roth (1997); Kinder and Palfrey (1993); McDermott (2002); Shadish, Cook,and Campbell (2002); Political Analysis 10:4 (Autumn 2002); American Behavioral Sci-entist 48:1 (January 2004); and the “ExperimentCentral” website.

5 Glaser (2003); Schuman and Bobo (1988).



More realistic settings are adopted by field experiments.6 One suchexperiment was conducted by Leonard Wantchekon in Benin in order todiscover whether clientelistic electoral appeals were superior to program-matic appeals in a country where clientelism had been the acknowledgedbehavioral norm since the inauguration of electoral politics. Wantchekonselected eight electoral districts, similar to each other in all relevantrespects. Within each district, three villages were randomly identified.In one, clientelistic appeals for support were issued by the candidate. In asecond, programmatic (national) appeals were issued by the same candi-date. And in a third, both sorts of appeals were employed. Wantchekonfound that the clientelist approach did indeed attract more votes than theprogrammatic alternative.7

Regrettably, experimentation on large organizations or entire societiesis usually impossible – by reason of cost, lack of consent by relevantauthorities, or ethical concerns. Experimentation directed at elite actorsis equally difficult, for elites are busy, well remunerated (and hence unre-sponsive to material incentives), and loathe to speak freely, for obviousreasons. However, researchers occasionally encounter situations in whicha nonmanipulated treatment and control approximates the circumstancesof a true experiment with randomized controls.8

Svante Cornell’s study of ethnic integration/disintegration offers a goodexample. Cornell is interested in the question of whether granting regionalautonomy fosters (a) ethnic assimilation within a larger national group-ing or (b) a greater propensity for ethnic groups to resist central directivesand demand formal separation from the state. He hypothesizes the latter.His study focuses on the USSR/Russia and on regional variation withinthis heterogeneous country. Cases consist of regionally concentrated eth-nic groups (N = 9), some of which were granted formal autonomy withinthe USSR and others of which were not. This is the quasi-experimentalintervention. Cornell must assume that these nine territories are equiva-lent in all respects that might be relevant to the proposition, or that anyremaining differences do not bias results in favor of his hypothesis.9 Thetransition from autocracy to democracy (from the USSR to Russia) pro-vides an external shock that sets the stage for the subsequent analysis.

6 Cook and Campbell (1979); Gerber and Green (2000); McDermott (2002).7 Wantchekon (2003).8 See, e.g., Brady and McNulty (2004) and Card and Krueger (1994).9 Whether this is really true need not concern us; it is Cornell’s claim, and it is a plausible

one.



Cornell’s hypothesis is confirmed: patterns of ethnic mobilization (thedependent variable) are consistent with his hypothesis in eight of the ninecases. Note that variation is available both spatially (across ethnic groups)and temporally.10

Another sort of Dynamic Comparison involves a synthetic (or com-posite) match. This is a relatively new approach to case comparison,so I follow Alberto Abadie and Javier Gardeazabal’s example closely.The authors are interested in understanding the effect of violent politi-cal conflict on economic growth. The problem is that political conflictsare extraordinarily diverse (e.g., in scope, endurance, intensity, and withrespect to various other factors that might impact growth performance),as are various background factors that characterize nation-states. Thus,the usual approach taken to this problem – the global cross-nationalregression – provides a rather “noisy” picture of causal relationships.11

Abadie and Gardeazabal define their cases as subnational regions withina single country, Spain, where each unit has a fairly high degree of auton-omy (and hence satisfies the condition of case independence). Their pri-mary interest is in a single case, the Basque country, where conflict hasbeen severe over the past several decades. (While moderate political con-flict between center and periphery is ubiquitous, it has not devolved intoviolence in other regions.) The authors note that a simple time-series anal-ysis could reveal the economic performance of the Basque region after theonset of ETA-sponsored terrorism. However, this “intervention” beganslowly in the 1960s and 1970s (there was no well-defined point of onset)and was coincident with a general economic downturn in Spain. Thus,temporal patterns are difficult to interpret.

As with traditional matching methods, Abadie and Gardeazabal iden-tify a series of covariates that might help to identify a territory or territoriesin Spain that is most similar to the Basque region with respect to variousfactors that might affect growth performance and yet has not experiencedviolent conflict. These covariates include real per capita GDP, investment,population density, the shape of the economy (e.g., agriculture, industry,and other sectors), as well as various measures of human capital. However,there is no perfect match for the Basque country among the sixteen other

10 Cornell (2002). Because there are nine cases, rather than just two, it is possible for Cornellto analyze covariational patterns in a probabilistic fashion. Thus, although one regiondoes not conform to theoretical expectation, this exception does not jeopardize his overallfindings.

11 Alesina et al. (1996).



Spanish regions. Rather than consigning themselves to a less-than-perfectcomparison, the authors instead construct a hypothetical case from thetwo cases that match relatively well with the Basque region, Madrid andCatalonia. Each is weighted according to the strength of the match (withthe Basque region) along the various dimensions noted earlier; the two arethen combined into a single case. This composite case is looked upon asproviding a best “control” case for the treatment case, the Basque region.“Our goal,” the authors explain, “is to approximate the per capita GDPpath that the Basque Country would have experienced in the absence ofterrorism. This counterfactual per capita GDP path is calculated as the percapita GDP of the synthetic Basque Country.”12 Based on this syntheticcounterfactual, the authors conclude that the Basque region experienced a10 percent loss in per capita GDP due to terrorist violence over the courseof two decades (the 1980s and 1990s). This is the economic effect of ter-rorism. One may question the generalizability of this result. Indeed, theauthors tread lightly on this matter, since their study is narrowly focusedon a single region. (Arguably, it is better classified as a single-outcomestudy, as discussed in the epilogue.) Even so, the technique is innovativeand is potentially applicable to many research contexts.

Because the classic experiment is indistinguishable in its essentials froma natural experiment (so long as there is a suitable control), I employthe term Dynamic Comparison for this set of experimental and quasi-experimental designs. Granted, observational settings that offer variationthrough time and through space are relatively rare. Where they exist,however, they possess the same attributes as the classic experiment andare rightly accorded pride of place among case study research designs.

Longitudinal Comparison

Occasionally, manipulated treatment groups are not accompanied by con-trols (untreated groups), a research design that I call Longitudinal Com-parison.13 This is so for three possible reasons. Sometimes, the effects ofa treatment are so immediate and obvious that the existence of a control

12 Abadie and Gardeazabal (2003: 117).13 Franklin, Allison, and Gorman (1997: 1); Gibson, Caldeira, and Spence (2002: 364);

Kinder and Palfrey (1993: 7); McDermott (2002: 33). This is sometimes referred toas a “within-subjects” research design. For additional examples in the area of medicalresearch, see Franklin, Allison, and Gorman (1997: 2); in psychology, see Davidson andCostello (1969).



is redundant. Consider a simple experiment in which participants areasked their opinions on a subject, then told a relevant piece of infor-mation about that subject (the treatment), and then asked again fortheir opinions. The question of interest in this research design is whetherthe treatment has any effect on the participants’ views, as measured bypre- and post-tests (the same question asked twice about their opinions).Evidently, one could construct a control group of respondents who arenot given the treatment; they are not told the relevant bit of informationand are simply re-polled for their opinion several minutes later. But itseems unlikely that anything will be learned from the treatment/controlcomparison, for opinions are likely to remain constant over the course ofseveral minutes in the absence of any intervention. In this circumstance,which is not at all rare in experiments focused on individual respondents,the control group is extraneous.

Another reason for dispensing with a control group is pragmatic. Inmany circumstances it simply is not feasible for the researcher to enlistsubjects to complement a treatment group. Recall that in order to serveas a useful control, untreated individuals must be similar in all relevantrespects to the treatment group. Consider the situation of the clinicalresearcher (e.g., a therapist) who “treats” a group or an individual. Shecan, within limits, manipulate the treatment and observe the responsefor this group or individual. But she probably will not be able to enlistthe services of a control group that is similar in all respects to the treat-ment group. In such circumstances, causal leverage comes from observ-ing changes (or lack of change) in the subject under study, as revealedby pre- and post-tests. This provides much more reliable evidence of atreatment’s true effect than a rather artificial comparison to some stipu-lated control group that is quite different from the group that has beentreated.14

Many experiments are time-consuming, intensive, expensive, and/orintrusive. Where the researcher’s objective is to analyze the effect of alengthy therapeutic treatment, for example, it may be difficult to monitora large panel of subjects, and it may be virtually impossible to do so in

14 Lundervold and Belwood (2000). Granted, if there is a group that has applied for treat-ment but has been denied (by reason of short capacity), then this group may be enlisted asa control. This is often found in studies focused on drug users, where a large wait-listedgroup is considered as a formal control for the treated group. However, most researchsituations are not so fortunate as to have a “wait-listed” group available for analysis.



an intensive fashion (e.g., with daily or weekly sessions between investi-gator and patient). It is not surprising that the field of psychology beganwith the experimental analysis of individual cases or small numbers ofcases – either humans or animals. Single-case research designs occu-pied most of the founding fathers of the discipline, including WilhelmWundt (1832–1920), Ivan Pavlov (1849–1936), and B. F. Skinner (1904–1990). Indeed, Wundt’s work on “hard introspection” dictated that hismost common research subject remained himself.15 Skinner once com-mented that “instead of studying a thousand rats for one hour each,or a hundred rats for ten hours each, the investigator is likely to studyone rat for a thousand hours.”16 Early psychologists were avid propo-nents of the experimental method, but their employment of this methodoften did not include a randomized control group, a relatively recentinvention.17

A final reason for neglecting a formal control in experimental researchdesigns is that it may violate ethical principles. Consider the case of apromising medical treatment that investigators are attempting to study.If there is good reason to suppose, ex ante, that the treatment will savelives, or if this becomes apparent at a certain point in the course of anexperiment, it may be unethical to maintain a control group – for, in nottreating them, one may be putting their lives at risk.

Regrettably, in most social science research situations the absence of aformal control introduces serious problems into the analysis. This is a par-ticular danger where human decision-making behavior is concerned, sincethe very act of studying an individual may affect her behavior. The subjectof our hypothetical treatment may exhibit a response simply because sheis aware of being treated (e.g., “placebo” or “Hawthorne” effects). In thissort of situation, there is virtually no way to identify causal effects unlessthe researcher can compare treatment and control groups. This is why,incidentally, single-case experimental studies are more common in natu-ral science settings (including cognitive psychology), where the researcheris concerned with the behavior of inanimate objects or with biologicallyinduced behavior.

In observational work (where there is no manipulated treatment), bycontrast, the Longitudinal Comparison is quite common. Indeed, most

15 Heidbreder (1933).16 Quoted in Hersen and Barlow (1976: 29). See also Franklin, Allison, and Gorman (1997:

23); Kazdin (1982: 5–6).17 Kinder and Palfrey (1993: 9).



case studies probably take this form. Wherever the researcher concentrateson a single case and that case undergoes a change in the theoretical variableof interest, a Longitudinal Comparison is in play.

Consider the introduction of compulsory voting laws in the Nether-lands just prior to the 1970 general election.18 If one is interested in theeffect of compulsory voting on turnout, this statutory change offers auseful quasi-experimental intervention. One has only to compare turnoutrates in 1970 with turnout rates in the previous election in order to deter-mine the causal effect of the law (turnout increased dramatically). Oneassumes, of course, that nothing else that might influence turnout ratesoccurred during this period and that the two elections are similar enough –in all ways that might affect turnout – that they can be meaningfullycompared. One also assumes more or less complete voter knowledge ofthe statutory change; otherwise there is, effectively, no treatment. Butthese assumptions, at least in this instance, seem relatively secure. Underthe circumstances, it is fair to regard such a study as a natural experi-ment, for the intervention of policy makers resembles the sort of inter-vention that might have been undertaken by investigators, if they had theopportunity.

Another example, somewhat more technical in nature, concerns theinterrelationship of monetary policy and economic fluctuations. This topicis undertaken by Milton Friedman and Anna Schwartz in their MonetaryHistory of the United States, a classic work in monetarist theory, recentlyreviewed by Jeffrey Miron, whose account I follow.19 The empirical heft ofthe book rests on four historical occasions on which the stock of moneychanged due to policy choices largely unrelated to the behavior of theeconomy (and hence exogenous to the research question). These fourinterventions were “the increase in the discount rate in the first half of1920, the increase in the discount rate in October 1931, the increase inreserve requirements in 1936–1937, and the failure of the Federal Reserveto stem the tide of falling money in 1929–1931.”20 Each was followed bya substantial change in the behavior of the stock of money, thus validatinga central pillar of monetarist theory.

Frequently, a study will incorporate several cases, each of whichincorporates a Longitudinal Comparison. This may be referred to asa series of case studies or, more extravagantly, as an “iterated natural

18 Jackman (1985: 173–5).19 Friedman and Schwartz (1963); Miron (1994).20 Miron (1994: 19).



experiment.”21 The key point is that the primary focus of comparisonin this type of research design is temporal, rather than spatial. Do not bemisled by the fact that there is more than one case; these cases are properlyregarded simply as multiple instances of the same intervention. If thereis an explicit spatial component to the comparison, then it is properlyclassified as a Dynamic Comparison (as already discussed) or a SpatialComparison, to which we now turn.

Spatial Comparison

A third archetypal research design involves a comparison between twocases (or groups of cases), neither of which experiences an observablechange on the variable of theoretical interest. I call this a Spatial Compar-ison, since the causal comparison is spatial rather than temporal. To besure, there is an assumption that spatial differences between the two casesare the product of antecedent changes in one (or both) of the cases. How-ever, because these changes are not observable – we can observe only theiroutcome – the research takes on a different, and necessarily more ambiv-alent, form. One cannot “see” X1 and Y interact; one can only observeresidues of their prior interaction. Evidently, where there is no variation inthe theoretical variable of interest, no experimental intervention can havetaken place, so this research design is limited to observational settings.

One interesting example of this sort of work focuses on intracoun-try differences in electoral system type. Here, researchers exploit the factthat in some countries, such as Germany, different electoral systems areemployed simultaneously. These are known as “mixed” electoral sys-tems, since they employ both proportional and first-past-the-post (single-member district) designs in a parallel fashion.22 In this setting, it is possiblefor researchers to observe differences in legislator behavior between thesetwo groups – those chosen by PR rules and those chosen by majoritarianrules – in order to discover clues about the conditioning role of electoralsystem design.23 Are members chosen from PR districts less susceptible topork barrel legislating? less sensitive to district preferences? less inclinedto district-level campaigning? more sensitive to cues from party leaders?

21 Gerring et al. (2005).22 Sometimes, the PR seats are employed to compensate for disproportional results at the

district level (e.g., in Germany); in other cases (e.g., Japan), the two systems operateindependently (Shugart and Wattenberg 2001).

23 Lancaster and Patterson (1990); Patzelt (2000); Stratmann and Baur (2002).



Another sort of comparison rests upon spatial comparisons acrossregions within a single country. Abhijit Banerjee and Lakshmi Iyer inves-tigate the long-term consequences of different property rights regimesacross various regions of India. The authors explain:

The British made different arrangements for the collection of [land] revenue indifferent areas, leading to different distributions of ownership rights. The differ-ent systems fall into three main groups: in landlord-based systems, the revenuecollection responsibilities for a number of villages was vested in a landlord whowas allowed to retain a part of the revenue he collected; in individual-based sys-tems the British government officers collected revenue directly from the actualcultivators without the intermediation of a landlord; in village-based systems, avillage community body bore the revenue responsibility.24

The main finding is that these property rights systems have strong effectson post-independence investments in agriculture and on measures of agri-cultural productivity in these areas. Varying patterns of colonial rule insti-tuted varying patterns of land tenure, leading to varying patterns of agri-cultural modernization.

In these two examples, one focused on contemporary electoral systemsand the other on secular-historical patterns of development, it is difficultto observe the effect of the intervention directly. It is not useful, that is, tolook at Germany before and after the installation of a mixed electoralsystem, because the situation prior to this electoral institution was notdemocratic. In the case of India, it would be very useful to observehow different areas evolved before and after the British instituted dif-ferent property rights systems; however, we lack the historical materialsto do so. Thus, in both situations the primary leverage scholars have onthe causal problem is spatial rather than temporal. Even so, variationsacross space (i.e., across different types of legislators or across differentregions) provide ample ground for reaching conclusions about probablecauses.

Counterfactual Comparison

A final research design available to case study researchers involves the useof a case (or cases) where there is no variation at all – either temporal orspatial – in the variable of interest. Instead, the intervention is imagined.

24 Banerjee and Iyer (2002: 5).



I call this a Counterfactual Comparison, since the thought experimentprovides all the covariational evidence that is available.25

Regrettably, there are quite a few instances in which a key variable oftheoretical interest does not change appreciably within the scope of anypossible research design. This is the classic instance of the dog that refusesto bark, and is often the only recourse for studies focused on “structural”variables – geographic, constitutional, sociological – which tend not tochange very much over periods that might feasibly be observed. Even so,causal analysis is not precluded. It did not stop Sherlock Holmes, andit does not stop social scientists. But it does lend the resulting investiga-tions the character of a detective story, for in this setting the researcher isconstrained to adopt a research design in which the temporal variation isimaginary and there is no spatial control.

Although it sounds rather exotic, this species of temporal reconstruc-tion is so common as to be second nature. Consider the following remarksof a journalist seeking to explain the rise of a Maoist insurgency in Nepalin the 1990s.

By 1994, Nepal’s Communists had split. One faction, led by Prachanda – whatwould become the Communist Party of Nepal (Maoist) – was kept out of theelections. Many Nepalis regard that as the crucial moment in the political historyof Communism in Nepal. Had the C.P.N. (M) been allowed to contest for power,it might never have resorted to war. By the time this was clear, however, it wastoo late.26

Although the writer follows journalistic standards by couching all anal-ysis in terms of expressed views (“many Nepalis regard . . .”), the coun-terfactual claim is clear. And it is plausible. Indeed, the elimination ofsuch claims would make much case-based social science – not to men-tion journalism and history – impossible, for without such counterfac-tual thought experiments writers would be constrained to analyze only

25 This definition of “counterfactual analysis” amplifies on Fearon (1991) and is narrowerthan others (e.g., Brown 1991), where the term is employed quasi-synonymously with“thinking.” This section thus argues against the contention of King, Keohane, and Verba(1994: 129) that “nothing whatsoever can be learned about the causes of the dependentvariable without taking into account other instances when the dependent variable takeson other values.” For additional work on counterfactual thought experiments in thehumanities and social sciences, see Cowley (2001); Elster (1978); Lebow (2000); andTetlock and Belkin (1996).

26 Sengupta (2005: 2).



situations where there was a change in the independent variable of inter-est (a Longitudinal Comparison), relevant variation across cases (a SpatialComparison), or both (a Dynamic Comparison).

One of the most famous observational studies without control orintervention was conducted by Jeffrey Pressman and Aaron Wildavskyon the general topic of policy implementation. The authors follow theimplementation of a federal bill, passed in 1966, to construct an air-port hangar, a marine terminal, a thirty-acre industrial park, and anaccess road to a major coliseum in the city of Oakland, California. Theauthors point out that this represented free money for a depressed urbanregion. There was every reason to assume that these projects would ben-efit the community, and every reason – at least from an abstract publicinterest perspective – to suppose that the programs would be speedilyimplemented. Yet, three years later, progress was agonizingly slow, andfew projects had actually been completed. The explanation provided bythe authors rests upon the bureaucratic complexities of the Americanpolity. Pressman and Wildavsky show that the small and relatively spe-cific tasks undertaken by the federal government necessitated the cooper-ation of seven federal agencies (the Economic Development Administra-tion [EDA] of the Department of Commerce, the Seattle Regional Officeof the EDA, the Oakland Office of the EDA, the General AccountingOffice, the Department of Health, Education, and Welfare [HEW], theDepartment of Labor, and the Navy), three local agencies (the mayorof Oakland, the city council, and the port of Oakland), and four pri-vate groups (World Airways Company, Oakland business leaders, Oak-land black leaders, and conservation and environmental groups). Thesefourteen governmental and private entities had to agree on at least sev-enty important decisions in order to implement a law initially passed inWashington.27 James Q. Wilson observes, “It is rarely possible to get inde-pendent organizations to agree by ‘issuing orders’; it is never possible todo so when they belong to legally distinct levels of government.”28 Theplausible counterfactual is that with a unitary system of government, thesetasks would have been accomplished in a more efficient and expeditiousfashion.

If one is willing to accept this conclusion, based upon the evidencepresented in Pressman and Wildavsky’s study, then one has made a causal

27 Pressman and Wildavsky (1973), summarized in Wilson (1992: 68).28 Wilson (1992: 69). For further discussion of methodological issues in implementation

research, see Goggin (1986).



inference based (primarily) on observational evidence drawn from caseswithout variation in the hypothesis of interest (the United States remainsfederal throughout the period under study, and there is no differencein the “degree of federalism” pertaining to the various projects understudy).

This style of causal analysis may strike the reader as highly tenuous, ongeneral methodological grounds. Indeed, it deviates from the experimen-tal paradigm in virtually every respect. However, before dismissing thisresearch design one must consider the available alternatives. One coulddiscuss lots of hypothetical research designs, but the only one that seemsrelatively practicable in this instance is the Spatial Comparison. That is,Pressman and Wildavsky might have elected to compare the United Statesto a similar country that does not have a federal system, but does grap-ple with a similar set of policies. Unfortunately, there is no really goodpaired case available for such a comparison. Countries that are unitaryand democratic tend to be quite different from the United States, and differin ways that might affect their policy-making processes. Britain is unitaryand democratic, but also quite a bit smaller in size than the United States.More importantly, it possesses a parliamentary executive, and this factoris difficult to disentangle from the policy process, posing serious issuesof spurious causality.29 At the end of the day, Pressman and Wildavsky’schoice of research methodology may have been the best of all availablealternatives. This is the pragmatic standard to which we rightly hold allscholars.

Ceteris Paribus

Thus far, I have set forth a typology intended to capture the covaria-tional properties of case study research designs. The typology answersthe question: what sort of variation is being exploited for the purposeof drawing causal conclusions from a small number of cases? I haveshown that such variation may be temporal and/or spatial, thus provid-ing four archetypal research designs: Dynamic Comparison, LongitudinalComparison, Spatial Comparison, and Counterfactual Comparison (seeTable 6.1).

I have also shown that these four research designs can be profitablyunderstood as deviations from the classic experiment. The Dynamic

29 For further examples and discussion of this sort of research design, see Weaver andRockman (1993).



Comparison exploits both spatial and temporal variation, and may bemanipulated (in which case it is a classic experiment) or nonmanipulated(observational). The Longitudinal Comparison exploits only temporalvariation, along the lines of an experiment without controls – thoughthe intervention may be manipulated or natural. The Spatial Comparisonexploits variation across cases observed cross-sectionally. The Counter-factual Comparison, finally, employs evidence that is nonempirical (imag-inary), but nonetheless aspires to the experimental ideal. This typology,while it does not exhaust the features of a good case study research design,summarizes the most important of these features in a compact form andmay serve as a useful template for the construction – and critique – ofcase study research.

Largely ignored in the previous discussion has been the ceteris paribuscaveat that undergirds all causal analysis. To say that X1 is a cause ofY is to say that X1 causes Y, all other things being equal. The ceterisparibus clause may be defined in many different ways; that is, the con-text of a causal argument may be bounded, qualified. But within thosestipulated boundaries, the assumption must hold; otherwise, causal argu-ment is impossible. All of this is well established, indeed definitional.Where it enters the realm of empirical testing is in the construction ofresearch designs that maintain ceteris paribus conditions along the twopossible dimensions of analysis. This means that any temporal variationin Y observable from t1 to t2 should be the product of X1 (the causalfactor of interest), rather than of any other confounding causal factor(designated as X2 in the previous discussion). Similarly, any spatial vari-ation in Y observable across the treatment and control cases should bethe product of X1, not X2. (The latter issue is sometimes referred to as“pre-treatment equivalence.”) These are the temporal and spatial com-ponents of the ceteris paribus assumption. Needless to say, they are noteasily satisfied.

It is here that the principal difference between experimental and non-experimental research is located. Donald Campbell’s cautionary tale ofthe state of Connecticut’s crackdown on speeding (a nonmanipulatedLongitudinal Comparison) serves as a reminder of how short-term trendsmay arise for reasons having nothing to do with the quasi-experimentaltreatment in question, leading to spurious conclusions. The story may bebriefly retold.30 Connecticut’s imposition of a harsh antispeeding law in

30 I offer here a highly abbreviated, selective account of Campbell’s well-known article(1968/1988).



1955 was followed by a dramatic fall in traffic fatalities in the followingyear, leading the governor (Ribicoff) to declare the law a success. Campbellshows, however, that this apparent decline could have been the productof several other factors having nothing to do with the change in statepolicy. These include (a) regression to the mean (1955 was an exception-ally bad year for traffic fatalities, so it is no surprise that 1956 would bean improvement); (b) long-term trends (traffic fatalities appear to havebeen declining for some time, nationally and in the state of Connecticut);and (c) a change in the baseline (an increasing number of cars on theroad).

Whether the research is experimental or not may make considerabledifference in the degree to which a given research design satisfies theceteris paribus assumption of causal analysis. First, where an interventionis manipulated by the researcher it is unlikely to be correlated with otherthings that might influence the outcome of interest. Thus, any changesin Y may be interpreted as the product of X1 and only X1, other factorsbeing held constant. Second, where the selection of treatment and controlcases is randomized, they are more likely to be identical in all respectsthat might affect the causal inference in question. Finally, in an experi-mental format the treatment and control groups are effectively isolatedfrom each other, preventing spatial contamination. This means that theceteris paribus assumption inherent in all causal inference is usually rel-atively safe in an experimental study. The control may be understood asreflecting a vision of reality as it would have been without the specifiedintervention.

All of these ceteris paribus assumptions are considerably more difficultto achieve in observational settings, as a close look at the foregoing exam-ples will attest.31 However, the point remains that they can be achievedin observational settings, and they can also be violated in experimen-tal settings. As J. S. Mill observed, “we may either find an instance innature suited to our purposes, or, by an artificial arrangement of circum-stances, make one. The value of the instance depends on what it is initself, not on the mode in which it is obtained. . . . There is, in short, nodifference in kind, no real logical distinction, between the two processes ofinvestigation.”32

31 See Campbell (1968/1988); Shadish, Cook, and Campbell (2002).32 Mill (1843/1872: 249).



It is the satisfaction of ceteris paribus assumptions, not the use ofa manipulated treatment or a randomized control group, that rightlyqualifies a research product as methodologically sound. Accordingly, themethodological issues of case study research may be conceptualized as aproduct of four paradigmatic styles of evidence, each of which calls fortha set of extremely important ceteris paribus assumptions.


7

Internal Validity: Process Tracing

In the previous chapter, the problem of internal validity was discussedfrom an experimental perspective. That is, the case study method wasunderstood as an attempt to satisfy the methodological criteria that definea well-designed experiment. To the extent that a single case, or a smallnumber of cases, exemplify a quasi-experimental design, the case studymethod is vindicated.

However, few case studies are truly experimental, in the sense of havinga manipulated treatment. This is because a manipulable treatment is usu-ally easy to replicate across multiple cases, thus providing a large-N cross-case research design. Moreover, among observational case studies, perfect“natural experiments” are rare. The observational world does not usu-ally provide cases with both temporal variation (making possible “pre”and “post” tests) and spatial variation (“treatment” and “control” cases)across variables of theoretical interest, while holding all else constant.Usually, there are important violations of the ceteris paribus assumption.

What this means is that case study research usually relies heavily oncontextual evidence and deductive logic to reconstruct causality within asingle case. It is not sufficient simply to examine the covariation of X1 andY, because there are too many confounding causal factors and because thelatter cannot usually be eliminated by the purity of the research designor by clever quantitative techniques (control variables, instrumental vari-ables, matching estimators, and the like).1 Thus, a “covariational” style ofresearch is usually insufficient to prove causation in a case study format.

1 Statistical techniques may be employed in the analysis of within-case evidence but not atthe level of across-case evidence, because the sample is too small (by definition).

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Process Tracing 173

Lest there be any confusion about this, it is important to emphasize thatthe pattern of covariation found between X1 (the causal variable of inter-est) and Y (the outcome of interest) is always central to case study analysis.(How could it be otherwise?) All causal analyses are covariational in thisobvious way. The point is that in case study research evidence pertainingto X1 and Y is often opaque, and must therefore be supplemented byanother form of analysis that has come to be known as process tracing.2

The hallmark of process tracing, in my view, is that multiple types ofevidence are employed for the verification of a single inference – bits andpieces of evidence that embody different units of analysis (they are eachdrawn from unique populations). Individual observations are thereforenoncomparable. Additionally, process tracing usually involves long causalchains. Rather than multiple instances of X1 → Y (the large-N cross-casestyle of research), one examines a single instance of X1 → X2 → X3 →X4 → Y. (Of course, this causal path may be much longer and morecircuitous, with multiple switches and feedback loops.)

In these respects, process tracing is akin to detective work. The maidsaid this; the butler said that; and the suspect was seen at the scene ofthe crime on Tuesday, just prior to the murder. Each of these facts isrelevant to the central hypothesis – that Jones killed Smith – but theyare not directly comparable to one another. And because they cannotbe directly compared, they cannot be analyzed in a unified sample. Themaid’s testimony is empirical, and it is certainly relevant, but it cannotbe reduced to standard dataset observations, and it is not meaningfullyunderstood within a formal research design.

Because this is a difficult “method” to wrap one’s mind around, webegin this chapter with a series of examples – diverse instances of processtracing at work in social science explanation. I then expatiate on thegeneral features of this form of analysis. In the conclusion, I try to addressthe knotty question of what characterizes a good (convincing) process-tracing analysis.

2 A number of vaguely synonymous terms might also be invoked, including causal-process observations, pattern matching, causal-chain explanation, colligation, congruencemethod, genetic explanation, interpretive method, narrative explanation, and sequentialexplanation. See Brady and Collier (2004); Danto (1985); George and Bennett (2005:Chapters 9–10); Goldstone (1991: 50–62); Hall (2003); Little (1995: 43–4); Roberts(1996); Scriven (1976); and Tarrow (1995: 472). Readers should be warned that myunderstanding of process tracing varies somewhat from that found elsewhere in the field,where it is sometimes equated with any investigation into causal mechanisms (George andBennett 2005).



Examples

Theda Skocpol’s renowned study of social revolution rests centrally onan in-depth examination of three key cases – Russia, China, and France.3

With respect to France, Skocpol identifies three general causal factorsleading to the breakdown of state authority in the eighteenth century:agrarian backwardness, international pressure, and state autonomy. Thesefactors, in turn, may be disaggregated into thirty-seven discrete steps thatconnect structural causes to the outcome of interest in this particularcountry-case. The entire argument is carefully mapped by James Mahoneyin a causal diagram, reproduced in Figure 7.1. Notice that each stage ofthe case study is qualitatively distinct, creating a series of nested researchdesigns. Thus, evidence for one link in the chain has no bearing on thenext (or previous) link.

As a second example, consider Pressman and Wildavsky’s study ofimplementation procedures, first introduced in the previous chapter.This study rests largely upon a demonstration of proximal relationshipsbetween key actors. The authors show, for example, that there is resis-tance to federal directives on the part of local political leaders whohave their own agendas and who often do not see eye to eye with theWashington bureaucrats assigned to implement the construction of pub-lic works projects in Oakland. Interviews with these actors, as well astheir own public statements, bolster the counterfactual reasoning of thebook. These local actors have different perspectives because they havedifferent constituencies, different organizational norms, and consequentlydifferent incentive structures. All of this, including the ability of the localactors to resist federal directives, may be considered as a product of theconstitutional and statutory structure of the American polity. Withoutfederalism, and without the local bureaucratic independence and multi-plication of agencies with overlapping jurisdictions that stems from a fed-eral constitution, things would have been very different. Again, a seriesof one-shot observations is enlisted to demonstrate a macro-causal claimapplying not just to the United States at large but to democratic politieseverywhere.

As a third example, consider Henry Brady’s reflections on his studyof the Florida election results in the 2000 presidential election.4 In thewake of this close election, at least one commentator – John Lott, an

3 Skocpol (1979). My account draws on Mahoney (1999).4 Brady (2004: 269–70).


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State Autonomy

InternationalPressure

Agrarian Backwardness

State Breakdown

figure 7.1. Skocpol’s explanation of the breakdown of the French state (1789). 1. Prop-erty relations prevent introduction of new agricultural techniques. 2. Tax system dis-courages agricultural innovation. 3. Sustained growth discourages agricultural innovation.4. Backwardness of French agriculture. 5. Weak domestic market for industrial goods.6. Internal transportation problems. 7. Population growth. 8. Failure to achieve indus-trial breakthrough. 9. Failure to sustain economic growth. 10. Inability to successfullycompete with England. 11. Initial military successes under Louis XIV. 12. Expansionistambitions of state. 13. French geographical location vis-a-vis England. 14. Sustained war-fare. 15. State needs to devote resources to both army and navy. 16. Repeated defeatsin war. 17. Creation of absolutist monarchy; decentralized medieval institutions persist.18. Dominant class often exempted from taxes. 19. State faces obstacles generating loans.20. Socially cohesive dominant class based on proprietary wealth. 21. Dominant class pos-sesses legal right to delay royal legislation. 22. Dominant class exercises firm control overoffices. 23. Dominant class is capable of blocking state reforms. 24. Dominant class resistsfinancial reforms. 25. Major financial problems of state. 26. State attempts tax/financialreforms. 27. Financial reforms fail. 28. Recruitment of military officers from privilegedclasses. 29. Military officers hold grievances against the crown. 30. Military officers iden-tify with the dominant class. 31. Military is unwilling to repress dominant class resistance.32. Financial crisis deepens. 33. Pressures for creation of the Estates-General. 34. King sum-mons the Estates-General. 35. Popular protests spread. 36. Conflict among dominant classmembers in the Estates-General; paralysis of old regime. 37. Municipal revolution; the oldstate collapses. Adapted from Mahoney (1999: 1166) after Skocpol (1979).

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economist – suggested that because several networks had called the statefor Gore prior to a closing of the polls in the panhandle section of the state,Republican voters may have been discouraged from going to the polls,and this in turn might have affected the margin (which was razor-thinand bitterly contested in the several months following the election). Lottreaches his conclusions on the basis of a regression analysis of turnoutin all sixty-seven Florida counties over the course of four presidentialelections, with a collection of controls (including fixed-year and countyeffects).5

Brady is unconvinced by the method, and by the results. Instead, hestitches together isolated pieces of evidence in an “ad hoc” fashion. Hebegins with the timing of the media calls – ten minutes before the closingof the polls in the panhandle. “If we assume that voters go to the polls atan even rate throughout the day,” Brady continues, “then only 1/72nd (tenminutes over twelve hours) of the [379,000 eligible voters in the panhan-dle] had not yet voted when the media call was made.” This is probably areasonable assumption. (“Interviews with Florida election officials and areview of media reports suggest that, typically, no rush to the polls occursat the end of the day in the panhandle.”) This means that “only 4,200people could have been swayed by the media call of the election, if theyheard it.” He then proceeds to estimate how many of these 4,200 mighthave heard the media call, how many of these who heard it were inclinedto vote for Bush, and how many of these might have been swayed, by theannouncement, to go to the polls in the closing minutes of the day. Bradyconcludes: “the approximate upper bound for Bush’s vote loss was 224and . . . the actual vote loss was probably closer to somewhere between 28and 56 votes.”6

Brady’s conclusions rest not on a formal research design but rather onisolated observations (both qualitative and quantitative) combined withdeductive inferences. How many voters “had not yet voted when themedia called the election for Gore? How many of these voters heard thecall? Of these, how many decided not to vote? And of those who decidednot to vote, how many would have voted for Bush?”7 These questions arevery different from those encountered in the foregoing studies of socialrevolution and policy implementation. Yet the approach has certain sim-ilarities insofar as Brady and colleagues enlist a set of observations thatdo not fall neatly into a standard research design and rely heavily on

5 Lott (2000).6 Brady (2004: 269–70).7 Ibid., 269.


Process Tracing 177

inferential reasoning, rather than on the sheer weight of the data, to reachtheir conclusions.

Often, process tracing is employed in conjunction with a standardresearch design – that is, as a supplementary tool. A good example isprovided by a recent paper that examines the behavior of the U.S. FederalReserve during the Great Depression. The central question is whetherthe Fed was constrained to adopt tight monetary policies because anydeviation from this standard would have led to a loss of confidence inthe nation’s commitment to the gold standard (i.e., an expectation of ageneral devaluation), and hence to a general panic.8 To test this propo-sition, Chang-Tai Hsieh and Christina Romer examine an incident inmonetary policy during the spring of 1932, when the Federal Reserveembarked on a brief program of rapid monetary expansion. “In just four-teen weeks,” the authors note, “the Federal Reserve purchased $936 mil-lion worth of U.S. government securities, more than doubling its holdingsof government debt.”9 To determine whether the Fed’s actions fosteredinvestor insecurity, Hsieh and Romer track the forward dollar exchangerate during the spring of 1932, which is then compared to the spot rate,using “a measure of expected dollar devaluation relative to the curren-cies of four countries widely thought to have been firmly attached togold during this period.”10 Finding no such devaluation, they concludethat the standard account is false – investor confidence could not haveconstrained the Fed’s actions during the Great Depression. This is thesort of empirical evidence that we are accustomed to, and it fits neatlyinto the Dynamic Comparison research design introduced in Chapter Six(the treatment case, the United States, is compared to several control casesduring the same period).

However, this conclusion would be questionable were it not bolsteredby additional evidence bearing on the probable motivations of the officialsof the Federal Reserve at the time. In order to shed light on this matter,the authors survey the Commercial and Financial Chronicle (a widelyread professional journal, presumably representative of the banking com-munity) and other documentary evidence. They find that “the leaders ofthe Federal Reserve . . . expressed little concern about a loss of credibil-ity. Indeed, they took gold outflows to be a sign that expansionary openmarket operations were needed, not as a sign of trouble.”11 The adjunct

8 This line of argumentation is pursued by Eichengreen (1992).9 Hsieh and Romer (2001: 2).

10 Ibid., 4.11 Ibid., 2.



evidence is instrumental in helping the authors to disconfirm a reigningtheory. Moreover, this evidence sheds light on a new theory about Fedbehavior during this critical era.

Our reading of the Federal Reserve records suggests that a misguided model ofthe economy, together with infighting among the twelve Federal Reserve banks,accounts for the end of concerted action. The Federal Reserve stopped largelybecause it thought it had accomplished its goal and because it was difficult toachieve consensus among the twelve Federal Reserve banks.12

This interpretation would not be possible (or at least would be highlysuspect) without the adjunct evidence provided by process tracing.

The Nature of Process-Tracing Evidence

These varied examples illustrate the most distinctive feature of process-tracing styles of research, namely, the noncomparability of adjacent piecesof evidence. All pieces of evidence are relevant to the central argument(they are not “random”), but they do not comprise observations in alarger sample. They are more correctly understood as a series of N = 1(one-shot) observations. Brady’s observation about the timing of themedia call – ten minutes before the closing of the polls – is followed by asecond piece of evidence, the total number of people who voted on thatday, and a third and a fourth. Although the procedure seems messy, we areoften convinced by its conclusions. It seems reasonable to suppose that,at least in some circumstances, inferences based on noncomparable obser-vations are more scientific than sample-based inferences, even though themethod borders on the ineffable. Our confidence rests on specific propo-sitions and specific observations; it is, in this sense, ad hoc. Indeed, thereappears to be little one can say, in general, about the research designsemployed by Skocpol, Pressman and Wildavsky, Brady, and Hsieh andRomer. While other methods can be understood according to their quasi-experimental properties, process tracing invokes a more complex logic,one analogous to detective work, legal briefs, journalism, and traditionalhistorical accounts. The analyst seeks to make sense of a congeries of dis-parate evidence, each of which sheds light on a single outcome or set ofrelated outcomes.

Note that although process tracing is always based on the analysis of asingle case, the ramifications of that case study may be generalizable, and

12 Ibid., 3.


Process Tracing 179

indeed may be quite broad in scope. Skocpol’s explanatory sketch enliststhe minutiae of French history to demonstrate a macro-theoretical accountpertaining to all countries that are wealthy and independent (noncolonies)in the modern era.

Note also that process-tracing evidence may be either qualitative orquantitative. Indeed, many of the examples just discussed involve evidencethat takes a predominantly quantitative form. However, because eachquantitative observation is quite different from the rest, they do not col-lectively constitute a sample. Each observation is sampled from a differentpopulation. This means that each quantitative observation is qualitativelydifferent. It is thus the noncomparability of adjacent observations, not thenature of individual observations, that differentiates the process-tracingmethod from standard research designs.

Note, thirdly, that because each observation is qualitatively differentfrom the next, the total number of observations in a study is usually inde-terminate. While the cumulative number of process-tracing observationsmay be quite large, because these observations are not well defined it isdifficult to say exactly how many there are. Noncomparable observationsare, by definition, difficult to count. In an effort to count, one may resortto lists of what appear to be discrete pieces of evidence. This approxi-mates the numbering systems employed in legal briefs. (“There are fifteenreasons why X is unlikely to have killed Y.”) But lists can always becomposed in multiple ways, and each piece of evidence carries a differentweight in the researcher’s overall assessment. So the total number of obser-vations remains an open question. We do not know, and by the nature ofthe analysis cannot know, precisely how many observations are presentin the studies by Skocpol, Pressman and Wildavsky, Brady, and Hsiehand Romer, or in other accounts such as Richard Fenno’s Homestyle andHerbert Kaufman’s The Forest Ranger.13

Process-tracing observations are not different examples of the samething; they are different things (“apples and oranges”). Consequently, itis not clear where one observation ends and another begins. They flowseamlessly together. We cannot reread the foregoing studies with the aidof a calculator and hope to discover their true N; nor would we gain anyanalytic leverage by so doing.

Quantitative researchers are inclined to assume that if observationscannot be counted, they must not be there, or – more charitably – that

13 Fenno (1978); Kaufman (1960).



there must be very few of them. Qualitative researchers may insist thatthey have many “rich” observations at their disposal, which provide themwith the opportunity for thick description. But they are unable to say,precisely, how many observations they have, or where these observationsare, or how many observations are needed for thick analysis. Indeed, theobservations themselves remain undefined.

This ambiguity is not necessarily troublesome, for the number of obser-vations in a process-tracing study does not bear directly on the usefulnessor truthfulness of that study. While the number of observations in a sam-ple drawn from a well-defined population contains information directlyrelevant to any inferences that might be based on that sample, the num-ber of observations in a non-sample-based study (assuming one couldestimate the N) has no obvious relevance to the validity of those infer-ences. Consider that if it were merely quantity that mattered, we mightconclude that longer studies, which presumably contain more observa-tions, are more valid than shorter studies. Yet it is laughable to assert thatlong narratives are more convincing than short narratives. It is the qualityof the observations and how they are analyzed, not the quantity of obser-vations, that is relevant in evaluating the truth claims of a process-tracingstudy. Indeed, the various noncomparable observations drawn upon ina given study are quite unlikely to be of equal importance, so merelycounting them gives no indication of their overall significance.

This brings us to a final characteristic of process tracing: it leans heavilyon general assumptions about the world, which may be highly theoreti-cal (nomothetic “laws”) or pre-theoretical (“common sense”). Preciselybecause of the absence of a formal research design, the researcher mustassume a great deal about how the world works. The process-tracingobservation makes sense only if it fits snugly within a comprehensibleuniverse of causal relations. I do not wish to imply that process-tracingevidence is “shaky”; indeed, much of it is quite matter-of-fact and close tothe ground. My point is simply that these facts are comprehensible onlywhen they can be ordered, categorized, “narrativized,” and this in turnrests upon a broad set of assumptions about the world.

The contrast with an ideal-typical experiment is revelatory. Where thereis a manipulated treatment and a control, a priori assumptions about theworld are minimized. There is not much to intuit in reaching conclusionsabout whether X1 causes Y (though the question of why X1 causes Y –the question of causal mechanisms – is often more complex). However, asone moves away from the experimental ideal, one perforce leans moreheavily on background assumptions about the way the world works.


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Insofar as these assumptions provide “priors” against which subsequentpieces of evidence can be evaluated, the analysis of noncomparable obser-vations takes on a Bayesian flavor.14 But the importance of contextualknowledge about the world also extends to other features of the analysis –the identification of viable alternatives (what, under the circumstances,were the options?), the playing out of various scenarios (counterfactuallogic), and so forth. The insufficiencies of the formal research design mustbe compensated for by natural wisdom – an intuitive “feel” for a situa-tion, usually gained through many years’ experience in that area, be it aforeign country, a historical era, or a medical specialty.

Thus, although background knowledge informs all causal analysis, itis more prominently on display in case studies where some portion of theevidence derives from process-tracing observations, for each observationmust be separately evaluated. Indeed, each noncomparable observationmay be considered to constitute a separate research design, requiring adifferent set of background assumptions.

The Usefulness of Process Tracing

Having defined the characteristic features of process tracing, we may nowinquire into its utility. What is it that makes a process tracing study (orportion of a study) useful and convincing? What is it that makes oneprocess tracing study better than another?

Let us say that process tracing is convincing insofar as the multiple linksin a causal chain can be formalized, that is, diagrammed in an explicit way(as a visual depiction and/or a mathematical model), and insofar as eachmicro-mechanism can be proven.

The first step seems fairly easy. If a causal relationship can be describedin prose, then it ought to be diagrammable, even if it cannot be captured ina precise mathematical model. Mahoney’s exegesis of Skocpol’s analysisof the French Revolution ought to be replicable for any similar account,that is, for any account that aims to explain a chain of causation withina single case. Granted, the identification of a discrete “step” in a causalchain is always a matter of judgment. The same causal process mightbe diagrammed in different ways, and there is no end, in principle, tothe infinite regress of causal mechanisms. And, to be sure, the act offormalizing a long set of concatenated inferences is apt to lead to some

14 George and Bennett (2005); Gill, Sabin, and Schmid (2005).



scary-looking diagrams. Robert Fogel’s causal diagram of the politicalrealignment occurring in mid-nineteenth-century America involves overfifty discrete steps and many more causal arrows (often bidirectional).15

Not a pretty picture. However, if this is Fogel’s best estimation of thecausal mechanisms, one can hardly deride the effort.

I do not mean to suggest that a formal diagram should replace a descrip-tion in prose. Indeed, one can scarcely imagine one without the other.What I mean to suggest is that the formal diagram is a useful heuris-tic, forcing the author to make a precise and explicit statement of herargument.

The second admonition is more complicated. Could all thirty-sevensteps in Skocpol’s argument about France (and about Russia and China)be tested? What would this mean? Note that if we isolate a single stepin this long argument, the nature of the causal analysis is now simplified.There is a single X1 and Y lying at the same level of analysis, whichmeans that we can understand that link within the rubric of a quasi-experimental framework, as discussed in the previous chapter. In princi-ple, a researcher engaged in a process-tracing analysis could propose aunique research design for each step at each stage of the analysis. Thirty-six research designs for thirty-seven steps, if they are all arrayed in a singlechain; many more if they are variously interconnected, as in Mahoney’sdiagram.

However, it is typical of case study research that these multiple linkscannot be tested in a rigorous fashion. Usually, the author is forced toreconstruct a plausible account on the basis of what I have called Coun-terfactual Comparison (what would have happened if X1 were different?).The reader will note a counterfactual style of analysis underlying each ofthe foregoing examples. This is what gives process tracing its highly deduc-tive quality. Typically, one finds oneself comparing states of affairs as theyexist to states of affairs as they might have existed. Upon the soundnessof each link, and the wealth of assumptions that inform each link, thesoundness of the entire enterprise rests. And because these assumptionsare often assumptions about a particular context – the context in whichthe case is situated – it is very difficult to assign a level of uncertainty tothat conclusion. A fortiori, it is difficult to arrive at a summary estimateof uncertainty for the entire analysis (based upon a long chain of causalmechanisms).

15 Fogel (1992: 233).


Process Tracing 183

Granted, one need not remain within a counterfactual mode of analysis.Sometimes, there is natural variation (temporal and/or spatial) in X1 and Ythat comes closer to the experimental ideal. And sometimes it is possibleto convert noncomparable observations into large-N research designs.Noncomparable bits of evidence can be transformed into comparablebits of evidence – that is, standardized “observations” – simply by gettingmore bits of evidence and coding them according to type. Thus, the non-comparable observations enlisted by Hsieh and Romer might have beenconverted into standardized (comparable) observations. For example, theauthors might have conducted a content analysis of the Commercial andFinancial Chronicle and/or of the Federal Reserve records. This wouldhave required coding sentences (or some other linguistic unit) accord-ing to whether they registered anxiety about a loss of credibility. Here,the sentence becomes the unit of analysis, and the number of sentencescomprises the total “N” in a quantitative research design.

In many instances, however, there is no suitable temporal and/or spatialvariation that approximates the experimental ideal, and/ or it is not possi-ble to convert noncomparable observations into comparable observationsso as to increase the sample size. It is difficult to see, for example, howHenry Brady’s research question could be generalized across additional(comparable) observations, given the absence of suitable surveys on elec-tion day 2000. In other circumstances, there may be little advantage tobe gained from the conversion of noncomparable to comparable observa-tions. In the Hsieh/Romer study, for example, it is not clear what would berealized from this sort of formalization. If there is no evidence whatsoeverof credibility anxiety in the documentary record, then the reader is notlikely to be more convinced by an elaborate counting exercise (coded as0, 0, 0, 0, 0, . . . ). More useful, I would think, are specific examples ofwhat the leaders of the Fed actually said, as provided by the authors ofthis study. Sometimes formalization is useful, and sometimes it is not.

We have already noted that a large number of standardized obser-vations are not always superior to a single noncomparable observation.Indeed, one of the foregoing examples, which pits Henry Brady’s processtracing against the large-N statistical analysis conducted by John Lott, isa good case for the superiority of an informal method over a formal one.The reader can probably think of many others. Thus, the N = 1 designa-tion that I have attached to process tracing should not be understood aspejorative. In some circumstances, one lonely observation (qualitative orquantitative) is sufficient to prove an inference. This is quite common, forexample, when the author is attempting to reject a necessary or sufficient



condition. If we are inquiring into the cause of Joe’s demise, and we knowthat he was shot at close range, we can eliminate suspects who were notin the general vicinity. One observation – say, a videotape from asurveillance camera – is sufficient to provide conclusive proof that a sus-pect was not, in fact, the killer, even though the evidence is neither quan-titative nor comparable to other pieces of evidence.

Recall, as well, that although many causal claims are typically nestedwithin a single process tracing account, not all of these are equally suspector equally important (for the overall argument). Two factors – theoreticalimportance and generally recognized priors – should determine the energywith which each claim is pursued. As a general rule, the need for a formallydesignated “research design” ends at the point where a causal conclusionbecomes obvious, as judged by the contextual evidence at hand or ourcommonsense knowledge of the world. Or, to put the matter differently,since the motivating goal of causal research is to determine the relationshipbetween X1 and Y, and since all such conclusions rest delicately upona skein of assumptions about how the world works, the purpose of aresearch design – a formal investigation into causes – is to supplementthat everyday knowledge wherever it appears weak. There is no point ininvestigating the obvious. This greatly simplifies the task of the processtracer. The researcher rightly focuses her attention on those links in thecausal chain that are (a) weakest and (b) most crucial for the overallargument.

Conclusion

To reiterate, our query regarding the validity of process tracing researchhas two very general answers: (1) clarify the argument, with all its atten-dant twists and turns (preferably with the aid of a visual diagram or formalmodel) and (2) verify each stage of this model, along with an estimate ofrelative uncertainty (for each stage and for the model as a whole). Sim-ple though it sounds, these two desiderata (and particularly the latter)are not always easy to accomplish. Process tracing evidence is, almost bydefinition, difficult to verify, for it extends to evidence that is nonexper-imental and cannot be analyzed in a sample-based format (by virtue ofthe incommensurability of individual bits of evidence).

Fortunately, there are several mitigating features of process tracingthat may give us greater confidence in results that are based, at least inpart, on this unorthodox style of evidence. First, process tracing is oftenemployed as an adjunct form of analysis – a complement to a formal


Process Tracing 185

research design (experimental or observational). Indeed, one way to thinkabout process tracing is as a cross-check, a triangulation, that can be – andought to be – applied to all results gained through formal methods. Studiesbased on a formal research design will sometimes note parenthetically thatthe account is consistent with “anecdotal” or “narrative” evidence, thatis, with evidence that falls outside the formal research design. It makessense of the statements made by the actors, of their plausible motives,and so forth. This is often extremely important evidence and deserves amore respectful label than “anecdotal” and a more revealing label than“narrative.” (What is the evidentiary status of a narrative?) In any case,process tracing, when employed in an adjunct fashion, is not intended tobear the entire burden of an empirical study. It offers supporting evidence.

Second, process tracing rests upon contextual assumptions and as-sumptions about how the world works. Insofar as there is a comfort-able fit between the evidence and the assumptions of a process tracingaccount, that account should pass muster. Granted, the reader of a pro-cess tracing account may not be in a position to judge the veracity ofan author’s conclusions that rest on the specific circumstances of a highlyparticular context. Even so, these conclusions may be vetted by those inti-mately familiar with that region, policy area, or historical era. So long assufficient documentation is included in the account, the verification of aprocess tracing study is eminently achievable. Therefore, even though itmay be impossible to arrive at a set of standardized methodological rules –thus depriving process tracing of the status of a “method” – we may haveconfidence in process tracing accounts once they have been vetted by suit-ably trained experts.

In sum, despite its apparently mysterious qualities, process tracinghas an important role to play in case-based social science. Whether itis employed in an adjunct capacity or whether the author’s conclusionsrest primarily on the analysis of noncomparable observations, it deservesan honored place in the tool kit of social science.


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Epilogue

Single-Outcome Studies

This book has understood case studies as a method for generalizing acrosspopulations (see Chapter Two). The population may be small or large,but the analysis is synecdochic. It infers a larger whole from a smallerpart. (Occasionally, where there is a very small population, the researchermay be able to study every case in the population intensively. In this rarecircumstance there is no inferential leap from sample to population.)

At times, however, the term “case study” may also refer to a piece ofresearch whose inference is limited to the case under study. This sort ofcase study may be characterized (loosely) as “idiographic” rather than“nomothetic” insofar as the objective of analysis is narrowly scoped toone particular (relatively bounded) unit. Arguably, this is not a case studyat all, since it is not a case of something broader than the case itself. Thus,I enlist a slightly different concept – the single-outcome study – as mytopic in this epilogue.

Formally, a single-outcome study refers to a situation in which theresearcher seeks to explain a single outcome for a single case. This out-come may register a change on Y – something happens. Or it may reflectstasis on Y – something might have happened but, in the event, does not.That is, the outcome may be “positive” or “negative.” The actual dura-tion of the outcome may be short (eventful) or long. A revolution (e.g., theAmerican Revolution) and a political culture (e.g., American political cul-ture) are both understood as outcomes, since they register distinct valuesfor a single case.

For the statistically minded, the single-outcome study may be under-stood as a study oriented toward explaining the point score for a singlecase rather than a range of values across a population of cases, or a range

187



of values occurring within a single case. One might also describe this asa “single-observation study,” for an outcome may be recorded on a sin-gle line of a rectangular dataset, registering only one value for each ofthe relevant variables. However, the term is awkward and also somewhatmisleading, since it implies that there are other comparable observationsadjacent to the observation of interest, which may or may not be true.Alternatively, one might refer to this format as an idiographic case study.However, this would imply the opposite – that the outcome under analy-sis is unique – which may or may not be true. Happily, the concept of anoutcome makes no a priori assumptions about neighboring phenomena;the outcome of interest may be routine or idiosyncratic.

By way of illustration, consider the following research questionsfocused on the contemporary welfare state (as measured by revenue orexpenditure levels as a share of total GDP):

(1) What explains the relatively weak American welfare state?(2) What explains welfare state development within the OECD?(3) What explains variation in U.S. welfare spending over time?(4) What explains variation in U.S. welfare spending across states?

Of these, only the first would be correctly classified as a study of a sin-gle outcome. Question #1 pertains to a single outcome because the case(the United States) is understood to have achieved a single, relatively sta-ble value on this dimension. There is implied variation on the dependentvariable (welfare state spending) across cases; indeed, the research ques-tion implicitly compares the United States to other countries. However,the researcher is not interested in explaining that variation; she is, instead,motivated to explain the point score of the United States.

By contrast, question #2 envisions the study of a population because itestablishes a range of variation – at least one differentiable outcome foreach OECD country; more if each case is observed over time. Question#3 recasts the first question from a single outcome to a population; itis focused on a range of comparable outcomes within a single case (theUnited States), defined temporally. Question #4 defines cases spatiallyrather than temporally; this is also a population.

It will be seen that a study focused on a single outcome must, of neces-sity, interrogate within-case evidence, and may therefore construct compa-rable observations within the case of primary interest. Thus, in answeringquestion #1, a researcher might employ strategies #3 and #4. Similarly,a single-outcome study might incorporate evidence drawn from adjacentcases (at the same level of analysis), that is, strategy #2. However, if the



purpose of this within-case and across-case evidence is to illuminate asingle outcome within a single case it is still appropriately classified as asingle-outcome study.

With these definitional matters under our belts, we may now proceed.What difference does it make whether an author is studying a case ofsomething broader than itself or a single outcome?1 What is the differ-ence between studying the U.S. welfare state (a) as an example of welfarestate development more generally and (b) as a topic in its own right? Inphilosophical circles, this may be understood as a distinction between acause (in general) and a cause in fact.2 In the one instance, the Ameri-can experience is enlisted to help explain something about welfare statedevelopment everywhere (or at least within the OECD). In the otherinstance, what we know about welfare states in general is enlisted to helpexplain one particular case. Virtually everything is identical about thesetwo topics except that the theoretical objective has shifted from macro tomicro.

Another example would be the distinction between crime (in general)and a particular crime. We might study a particular crime in order toelucidate some more general feature of crime in a society. This would be acase study. Or we might study the details of a particular crime – as well asmore general features of crime – in order to understand who shot Joe,and why. This would be a single-outcome study. It is one thing to explaina rise in crime, and quite another to explain why Joe was killed. In thischapter, we shift gears from the first sort of explanation to the second.

I begin by discussing the utility of single-outcome studies and the differ-ent types of argumentation and causal logic that they embrace. I proceedto discuss the methodological components of the single-outcome study,which may be reduced to three angles: nested analysis (large-N cross-case analysis), most-similar analysis (small-N cross-case analysis), andwithin-case analysis (evidence drawn from the case of special interest).The chapter concludes with a discussion of a common difficulty encoun-tered by single-outcome analysis – reconciling cross-case and within-caseevidence, both of which purport to explain the outcome of interest.

It is important to bear in mind that this chapter focuses on the distinc-tive methodological features of single-outcome studies. I leave aside, ortreat lightly, issues that are equally relevant to case studies. Thus, wherever

1 For discussions of the methodological issues arising from the attempt to explain a singleevent, see Goertz and Levy (forthcoming) and Levy (2001).

2 Hart and Honore (1959).



I choose not to expatiate on a point, the reader may assume that whatI have said in previous chapters of this book also applies to the single-outcome study.

Why Study Single Outcomes?

Methodologists have traditionally taken a dim view of single-outcomestudies. Case studies are bad enough (as reviewed in Chapter One). Single-outcome studies are, by implication, even worse. Arguably, we are betteroff focusing our efforts on things in general rather than on highly specificthings. Nomothetic research is more profitable, theoretically speaking,and also – usually – more falsifiable.3 (The reader will note that on animagined idiographic-nomothetic scale, single-outcome studies lie at oneend and cross-case studies at the other extreme, with case studies – theprimary focus of this book – in the middle.)

Even so, there are many situations in which one might wish to under-stand specific circumstances, rather than circumstances in general. PaulineYoung clarifies that the term “social case work” often refers to specificcontexts.

In social case work we do not gather data in order to compare, classify, andanalyze with a view to formulating general principles. We gather the data case bycase in order to make a separate, differential diagnosis, with little or no regardfor comparison, classification, and scientific generalization. The diagnosis is madewith a view to putting treatment into operation in this particular case.4

While scholars of international relations have an interest in wars, they arealso interested in the causal factors that led to specific wars, particularlybig wars with large consequences.5 Every country, every region, everybusiness, every era, every event, every individual – for that matter, everyphenomenon that a substantial number of people care about – inspires itsown single-outcome research agenda. Citizens of Denmark wonder whyDenmark has turned out the way it has. Chinese-American immigrantswonder why this group exhibits certain sociological and political patterns.Every public figure of note or notoriety sooner or later becomes the subjectof a biography or autobiography. Indeed, the vast majority of the booksand articles published in a given year are single-outcome analyses.

3 Goldthorpe (1997); King, Keohane, and Verba (1994); Lieberson (1985, 1992).4 Young (1939: 235–6).5 Levy (2002b).



Social scientists, like lay citizens, are often interested in how theirchosen subject plays out in their country of origin. Thus, Americaneconomists study the American economy; American sociologists studyAmerican society; and American political scientists study American poli-tics. Of course, they may study particular aspects of these broad subjects;the point is that their concern in this genre of work is not a class of out-comes but rather a particular outcome or a set of outcomes pertaining toa particular country. It is not merely idle curiosity that fuels this sort ofresearch. Understanding who we are – as individuals and as communities –rests, in part, on an understanding of what factors have made us whowe are.

Why is the United States a welfare state laggard?6 What caused WorldWar One?7 Why did the U.S. Federal Reserve not pursue a more expan-sionary monetary policy during the Great Depression?8 What accountsfor the rise of the West?9 Why have growth rates in Botswana beenso extraordinary over the past four decades?10 How can the inceptionand growth of the European Union be explained?11 Why did PresidentTruman choose to employ nuclear weapons against Japan?12 What arethe causes of the terrorist attack on the World Trade Center that occurredon September 11, 2001?13 Questions of this kind are not at all unusualin the social sciences.

Moreover, there are circumstances in which we can explain a particu-lar outcome more easily than we can a class of outcomes. This is apt tobe true when the cross-case evidence available on a topic is scarce andheterogeneous. Consider the following two questions: (1) why do socialmovements happen? and (2) why did the American civil rights move-ment happen? The first question is general, but its potential cases arefew and extremely heterogeneous. Indeed, it is not even clear how onewould construct a universe of comparable cases. The second question isnarrow, but – I think – answerable. I hasten to add that quite a number offactors may provide plausible explanations for the American civil rightsmovement, and the methodological grounds for distinguishing good from

6 Alesina and Glaeser (2004).7 Goertz and Levy (forthcoming).8 Hsieh and Romer (2001).9 McNeill (1991); North and Thomas (1973).

10 Acemoglu, Johnson, and Robinson (2003).11 Moravcsik (1998).12 Alperovitz (1996).13 9/11 Commission Report (2003).



bad answers is not entirely clear. Even so, I find work on this idiographicquestion more convincing than work on the nomothetic question of whatcauses social movements.14

Return for a moment to questions raised in our previous discussion:(1) what causes crime? and (2) who killed Joe? One can easily imaginepropositions about the latter that are more secure than propositions aboutthe former. Arguably, criminal justice verdicts are more dependable thancriminal justice studies. We are able to convict or acquit in most caseswith a high degree of certainty, while we are often unable to dispensewith general questions about crime.

In sum, single-outcome analysis is both intrinsically valuable (becausewe wish to know about such occurrences) and, at least in some circum-stances, methodologically tractable. There must, then, be some generalprinciples upon which single-outcome analysis rests.

The Argument

As with case study research, it is essential for the researcher to specifya clear hypothesis, or at least a relatively clear research question. Thispoint deserves special attention in light of the seeming obviousness ofresearch connected with a particular event. If one is studying World WarOne, it seems self-evident that the researcher will be attempting to explainthis historical fact. The problem is that this is a very immense fact, andconsequently can be seen from many angles. “Explaining World War One”could mean explaining (a) why the war occured (at all); (b) why it brokeout in 1914; (c) why it broke out on June 28, 1914; (d) why it brokeout in the precise way that it did (i.e., shortly after the assassination ofArchduke Ferdinand); (e) why it was prosecuted in the manner that itwas, and so forth. Option (a) suggests – but does not mandate – a focuson antecedent (structural, distal) causes, while the other options suggesta focus on proximate causes (of many different kinds). Evidently, the waythe research question is posed is likely to have an enormous impact onthe chosen research design, not to mention the sort of conclusion that theauthor reaches. While this is true of any study – cross-case, case study, orsingle-outcome – it is particularly true for studies that focus on individualoutcomes. Thus, single-outcome analysis requires the author to work hardto define and operationalize what it is that she is trying to explain.

14 Contrast McAdam (1988) with McAdam, Tarrow, and Tilly (2001). On this generalpoint, see Davidson (1963).



Andrew Bennett begins his book-length study by outlining a generalquest: “to explain the rise of Soviet military interventionism in the 1970s,its fall in the 1980s, and its reprise in the form of Russia’s interventions inthe former Soviet republics and Chechnya in the 1990s.”15 Subsequently,Bennett lays out more nuanced indicators of interventionism. This esca-lation ladder includes the following steps: “a) shipment of arms to theclient regime; b) transport of non-Soviet troops to or in the client regime;c) direct supply of non-Soviet troops on the front; d) deployment of Sovietmilitary advisers in the war zone; e) military aid to allied troops in ‘proxy’interventions; f) use of Soviet troops in combat roles; g) massive scale inthe above activities; h) use of Soviet commanders to direct the militarycampaign; and i) use of Soviet ground troops.”16 This is a good exampleof how a general topic can be operationalized in a clear and falsifiablemanner.

Granted, many single-outcome studies do not have clearly defined out-comes. A general history of World War One may be about many thingsrelated to World War One. A general history of Denmark is likely tofocus on many things related to Denmark. A biography of Stalin is aboutmany things related to Josef. There is nothing wrong with this traditionalvariety of historical, ethnographic, or journalistic narrative. Indeed, mostof what we know about the world is drawn from this genre of work.(My bookshelves are filled with them.) However, we must also take noteof the fact that this sort of study is essentially unfalsifiable. It cannotbe proven or disproven, for there is no argument per se. It is causalanalysis only in the loosest sense. My injunction for a clear hypothesisor research question is applicable only if the objective of the writer iscausal-explanatory in a stricter, and more scientific, sense. It is this sort ofwork – a small minority of single-outcome studies – that I am concernedwith.

Not only the outcome, but also the causal factor(s) of interest, must beclearly specified. Again, one finds that this is often more complicated insingle-outcome analysis than it is in case study analysis, precisely becausethere is no larger field of cases to which the inference applies. Douglass

15 Bennett (1999: 1). I shall assume that these are three discrete and relatively noncompa-rable outcomes, rather than a range of outcomes along a single dimension. If the latter,then Bennett’s study would be more appropriately classified as the study of a populationrather than of a series of single outcomes.

16 Ibid., 15. The book focuses at the high end of this scale; the entire scale is repro-duced here to illustrate how sensitive indicators may be developed in single-eventcontexts.



North and his colleagues take note of the following traditional argumentspertaining to U.S. economic history.

1. British policy was vindictive and injurious to the colonial economyafter 1763.

2. The railroad was indispensable for American economic growth.3. Speculators and railroads (through land grants) monopolized the

best western lands in the nineteenth century, slowed down the west-ward movement, adversely affected the growth of the economy, andfavored the rich over the poor.

4. In the era of the robber barons, farmers and workers wereexploited.17

In looking closely at these arguments, North and colleagues observe thatthey are ambiguous because there is no clearly specified counterfactual.The authors therefore revise them as follows:

1. British policies were restrictive and injurious to the colonial econ-omy after 1763, compared with what would have taken place hadthe colonies been independent during these years; or more precisely,income of the colonies under British rule after 1763 was less thanit would have been had the colonists been free and independent.

2. Income in the United States would have been reduced by more than10 percent had there been no railroads in 1890.

3. A different (but specified) land policy would have led to more rapidwestward settlement in the nineteenth century, a higher rate of eco-nomic growth, and a more equal distribution of income.

4. In the absence of the monopolistic practices of the robber barons,farm income and real wages of manufacturing workers would havebeen significantly higher.18

Here is a set of falsifiable hypotheses. They specify an outcome, an alter-native outcome, and a causal factor that is thought to be accountable for(imagined) variation across those outcomes.

Another point to be aware of is that the way in which an outcomeis defined is likely to determine the extent to which it is comparable toother cases. Specifically, the more detailed the outcome – the more it istailored to the circumstances of a specific country, group, or individual –the more difficult it will be to make reference to instances outside the area

17 North, Anderson, and Hill (1983: 2–3).18 Ibid., 3.



of interest. If the case of special interest is defined too idiosyncratically itwill no longer be a case of anything; that is, it will no longer be comparable(except in the most anodyne and unilluminating way) to other cases. Sinceone’s objective is to explain that outcome, and not others, this is notnecessarily problematic. However, it does mean that the author will berestricted to evidence drawn from that particular case. This is a seriousrestriction and limits the falsifiability of any such proposition, since itcannot be tested across other venues.

Causal Logic

Before going any further it is important to point out that the causallogic employed in case studies is often quite different from that of single-outcome studies, and this difference stems from their different objectives.Because the case study is focused on developing an explanation for somemore general phenomenon it usually focuses on a particular causal factor,X1, and its relationship to a class of outcomes, Y. It usually culminates inan X1/Y–centered hypothesis which explains some amount of variationacross instances of Y.

While it is a reasonable objective to seek to explain a small degree ofvariation across a wide range of cases, it is not a very reasonable objectiveto explain a small degree of variation across one outcome. Wherever astudy focuses on a single outcome, the reader quite naturally wants toknow everything, or almost everything, about the causes of that outcome(leaving aside the obvious background factors that every causal argumenttakes for granted). Thus, single-outcome studies usually seek to develop amore or less “complete” explanation of an outcome, including all causesthat may have contributed to it, X1−N.

Single-outcome studies make extensive use of necessary and sufficientconditions – deterministic ways of understanding causal relations. In casestudies, by contrast, researchers usually assume probabilistic causal rela-tions. The simple reason for this is that a general outcome encompassingmultiple cases is less likely to conform to an invariant law. While therewere undoubtedly necessary conditions for the occurrence of World WarOne, there is debate among scholars over the existence of necessary con-ditions pertaining to wars in general. (Only one such necessary conditionhas been proposed – nondemocracy – and it is hotly contested.)19 As arule, the larger the class of outcomes under investigation, the more likely

19 Brown, Lynn-Jones, and Miller (1996).



it is that there will be exceptions, in which case the scholar rightly con-ceptualizes causes as probabilistic rather than necessary and/or sufficient.

Relatedly, because case studies seek general causes they tend to focus onstructural causal factors. Because single-outcome studies seek the causesof specific outcomes, they often focus on contingent causal factors – forexample, leadership, decisions, or other highly proximate factors. Theassassination of Archduke Ferdinand is a plausible explanation of WorldWar One, but not of wars in general.20 It might of course be enlistedas an example of a more general explanation, but the author’s emphasiswould then shift to a more general factor (e.g., “triggering events”). Propernouns are often embraced in the single-outcome study, while they mustbe regarded as examples of something else in the case study.

However, it would be wrong to conclude that because unique causes areadmissible in single-outcome studies, they are also preferable. One doesnot imply the other. That is, an individual outcome may be the productof a very general cause (a “law”). Or it may not. There is no reason topresume that a case chosen for special study is different from a broaderclass of cases merely because it happens to form the topic of interest.A study of the American welfare state should not assume, as a point ofdeparture, that the causal dynamics of welfare state development in theUnited States are fundamentally different from those unfolding in Europeand elsewhere in the world. An inquiry into a particular murder shouldnot assume that the causes of this murder are any different from the causesof other murders, and so forth. The question of similarity and differencein causal analysis – the comparability of cases – is thus rightly left open,a matter for investigation.21 To clarify, single-outcome research designsare open to idiographic explanation in a way that case study research isnot. But single-outcome researchers should not assume, ex ante, that thetruth about their case is contained in factors that are specific to that case.

Granted, there is an affinity between single-outcome analysis and idio-graphic explanations insofar as the outcomes that attract the most atten-tion from social scientists are apt to be outcomes that are nonroutine – out-comes that don’t fit into standard explanatory tropes. (I expatiate on thispoint in the conclusion). However, the “uniqueness” of a historian’s (or

20 Lebow (2000–01); Lebow and Stein (2004).21 Granted, some single-event analyses have as their primary objective a search for distinc-

tiveness. Thus, the researcher’s question might be “What is different about X (Denmark,the United States, etc.)?” However, this is an essentially descriptive question, while ourconcern in this chapter is with causal inference.



political scientist’s or sociologist’s) chosen topic is a poor point of depar-ture, encouraging a prejudiced style of investigation into the actual causesof that outcome – which may be more routine than is generally realized.

Analysis

The analysis of a single outcome (a single outcome for a given case) maybe approached from three different angles. The first, which I refer to(following Evan Lieberman) as nested analysis, employs cross-case anal-ysis from a large sample in order to better understand the features of anindividual outcome. The second, known most commonly as most-similaranalysis, employs cross-case analysis within a small sample (e.g., two orthree cases). The third, known generically as within-case analysis, drawson evidence from the case of special interest.22

The latter two methods are quintessentially case study methods, so mydiscussion of these topics builds on arguments from previous chapters.In particular, I draw on the experimental template of case study meth-ods set forth in Chapter Six (see Table 6.1). There, I argued that all casestudies could be understood as variants of four archetypal methods: theDynamic Comparison, which mirrors the paradigmatic laboratory exper-iment (exploiting both temporal and spatial variation); the LongitudinalComparison, which employs only temporal variation but is similar indesign to the experiment without control; the Spatial Comparison, whichemploys only variation through space (purporting to measure the out-come of interventions that occurred at some point in the past, but thatare not directly observable); and the Counterfactual Comparison, whichrelies on imaginary variation (i.e., where the researcher seeks to replicatethe circumstances of an experiment in her head or with the aid of someformal model).

For purposes of discussion, I return to the question raised at the outsetof this chapter: Why does the United States have a relatively small welfarestate? This outcome is operationalized as aggregate central governmentrevenue as a share of GDP. As previously, research on this topic maybe either hypothesis-generating (Y-centered) or hypothesis-testing (where

22 Note that the task of “case selection” in single event analysis is already partiallyaccomplished: one has identified at least one of the cases that will be subjected to inten-sive study. It should also be noted that case analysis may be assisted by formal models(e.g., Bates et al. 1998) or statistical models (e.g., Houser and Freeman 2001). Here, I amconcerned only with the evidentiary basis (the sorts of evidence that might be mustered)for such an analysis.



there is a specific X1/Y proposition that the researcher is intending toprove or disprove). How, then, might (a) nested analysis, (b) most-similaranalysis, and (c) within-case analysis be applied to this classic researchquestion?

Nested AnalysisA nested analysis presumes that the researcher has at her disposal a large-N cross-case dataset containing variables that measure the outcome andat least some of the factors that might affect that outcome. With this infor-mation, the researcher attempts to construct a general model of the phe-nomenon that applies to the broader sample of cases. This model, whichmay be cross-sectional or time-series cross-sectional, is then employed toshed light on the case of special interest.23

Let us begin at the descriptive level. How exceptional (unique) is theAmerican state? The first section in Table E.1 lists all minimally demo-cratic countries for which central government expenditure data is avail-able in 1995 (N = 77), along with their normalized – “Z” – scores (stan-dard deviations from the mean). Here, it will be seen that the UnitedStates has a moderately low score – seventeenth out of seventy-seven –but not an extremely low score, relative to other democratic polities. Soviewed, there is little to talk about; the American case is only moderatelyexceptional.

However, the traditional way of conceptualizing the question of Amer-ican exceptionalism utilizes an economic baseline to measure the size ofwelfare states. The presumption is that richer, more developed societiesare likely to tax and spend at higher rates (“Wagner’s Law”). This way ofviewing things may be tested by regressing government spending againstGDP per capita (natural logarithm), as follows:

Expenditure = 4.89 + 3.10GDPpc(E.1)

R2 = .1768 N = 77

The residuals produced by this analysis for all seventy-seven cases arelisted in the second column of Table E.1. Here, it will be seen that theUnited States is indeed a highly exceptional case. Only four countries havehigher negative residuals. Relative to its vast wealth, the United States isa very low spender.

23 Lieberman (2005a). Coppedge (2002) employs the term “nested induction,” but the gistof the method is quite similar.


tabl

eE

.1.

Thr

eene

sted

anal

yses

ofth

eU

.S.w

elfa

rest

ate

Des

crip

tive

Ana

lysi

sB

ivar

iate

Ana

lysi

sM

ulti

vari

ate

Ana

lysi

s

Cou

ntry

Exp

.Z

scor

eC

ount

ryR

es.1

Cou

ntry

Res

.2

1.C

olom

bia

13.3

7−(

1.71

)1.

Sout

hK

orea

−17.

151.

Sout

hK

orea

−18.

392.

Indi

a14

.84

−(1.

57)

2.A

rgen

tina

−16.

732.

Tha

iland

−16.

713.

Dom

inic

anR

ep.

15.3

9−(

1.51

)3.

Col

ombi

a−1

5.62

3.B

aham

as−1

5.97

4.Pa

ragu

ay15

.41

−(1.

51)

4.B

aham

as−1

5.05

4.Tu

rkey

−14.

045.

Arg

enti

na15

.75

−(1.

48)

5.U

nite

dSt

ates

−14

.85

5.M

auri

tius

−12.

336.

Tha

iland

15.7

8−(

1.47

)6.

Mex

ico

−13.

906.

Para

guay

−9.9

97.

Mex

ico

15.9

2−(

1.46

)7.

Tha

iland

−13.

757.

Icel

and

−8.9

88.

Sout

hK

orea

16.5

2−(

1.40

)8.

Para

guay

−12.

818.

Can

ada

−8.4

89.

Nep

al16

.54

−(1.

40)

9.D

omin

ican

Rep

.−1

2.25

9.N

epal

−8.2

510

.Mad

agas

car

17.3

9−(

1.32

)10

.Ven

ezue

la−1

1.63

10.A

rgen

tina

−7.8

111

.Phi

lippi

nes

17.9

3−(

1.26

)11

.Sw

itze

rlan

d−1

1.33

11.C

osta

Ric

a−7

.15

12.V

enez

uela

18.5

7−(

1.20

)12

.Chi

le−1

1.14

12.P

eru

−6.8

013

.Bah

amas

19.0

3−(

1.16

)13

.Can

ada

−10.

4913

.New

Zea

land

−6.0

714

.Per

u19

.07

−(1.

15)

14.A

ustr

alia

−10.

3214

.Dom

inic

anR

ep.

−5.7

015

.Chi

le19

.85

−(1.

08)

15.P

eru

−9.7

215

.Mad

agas

car

−5.4

716

.Bol

ivia

21.1

0−(

0.95

)16

.Mal

aysi

a−8

.82

16.L

ithu

ania

−5.1

217

.Uni

ted

Stat

es21

.72

−(0

.89)

17.P

hilip

pine

s−8

.60

17.M

alay

sia

−5.0

418

.Mal

aysi

a21

.98

−(0.

87)

18.I

ndia

−8.4

518

.Col

ombi

a−4

.98

19.T

urke

y22

.23

−(0.

84)

19.C

osta

Ric

a−7

.66

19.G

reec

e−4

.71

20.C

osta

Ric

a22

.43

−(0.

82)

20.T

urke

y−7

.23

20.S

t.V

ince

nt/G

rena

da−4

.33

21.P

akis

tan

22.8

0−(

0.79

)21

.Mau

riti

us−6

.82

21.T

rini

dad/

Toba

go−4

.15

22.M

auri

tius

23.2

6−(

0.74

)22

.Nep

al−4

.99

22.I

ndia

−3.4

123

.Mon

golia

24.3

8−(

0.63

)23

.Pan

ama

−4.9

823

.Pan

ama

−3.3

6

(con

tinu

ed)

199


tabl

eE

.1(c

onti

nued

)

Des

crip

tive

Ana

lysi

sB

ivar

iate

Ana

lysi

sM

ulti

vari

ate

Ana

lysi

s

Cou

ntry

Exp

.Z

scor

eC

ount

ryR

es.1

Cou

ntry

Res

.2

24.P

anam

a24

.71

−(0.

60)

24.B

oliv

ia−4

.87

24.G

rena

da−3

.25

25.C

anad

a25

.04

−(0.

57)

25.M

adag

asca

r−4

.44

25.L

atvi

a−3

.17

26.L

ithu

ania

25.2

2−(

0.55

)26

.Ice

land

−3.4

626

.Aus

tral

ia−2

.99

27.A

ustr

alia

25.3

3−(

0.54

)27

.Rus

sia

−3.4

427

.Chi

le−2

.79

28.R

ussi

a25

.39

−(0.

53)

28.G

erm

any

−3.1

028

.Fiji

−2.4

429

.Sw

itze

rlan

d26

.64

−(0.

41)

29.L

ithu

ania

−2.8

329

.Ire

land

−1.9

930

.Gre

nada

28.1

1−(

0.27

)30

.Uru

guay

−2.7

830

.Mex

ico

−1.6

431

.Tri

nida

d/To

bago

28.1

3−(

0.26

)31

.New

Zea

land

−2.6

731

.Den

mar

k−1

.24

32.F

iji28

.61

−(0.

22)

32.T

rini

dad/

Toba

go−2

.60

32.L

uxem

bour

g−1

.19

33.U

rugu

ay28

.88

−(0.

19)

33.G

rena

da−1

.49

33.M

ongo

lia−0

.97

34.S

t.V

ince

nt/G

rena

da29

.16

−(0.

16)

34.C

ypru

s,G

reek

−1.4

034

.Nor

way

−0.9

535

.Pap

uaN

ewG

uine

a29

.21

−(0.

16)

35.P

akis

tan

−1.3

135

.Alb

ania

−0.8

036

.Sri

Lan

ka29

.33

−(0.

15)

36.G

reec

e−1

.07

36.B

oliv

ia−0

.77

37.V

anua

tu29

.34

−(0.

15)

37.F

iji−0

.61

37.V

enez

uela

−0.4

838

.Sou

thA

fric

a30

.57

−(0.

03)

38.S

outh

Afr

ica

0.11

38.C

ypru

s,G

reek

−0.1

739

.Alb

ania

31.0

1(0

.02)

39.S

t.V

ince

nt/G

rena

da0.

2039

.Uni

ted

Stat

es−

0.14

40.R

oman

ia31

.78

(0.0

9)40

.Spa

in0.

5840

.Van

uatu

−0.0

741

.Lat

via

32.2

0(0

.13)

41.M

ongo

lia1.

0041

.Est

onia

−0.0

342

.New

Zea

land

32.3

2(0

.15)

42.I

rela

nd1.

3642

.Sw

itze

rlan

d0.

0443

.Cyp

rus,

Gre

ek32

.60

(0.1

7)43

.Lux

embo

urg

1.66

43.S

pain

0.05

44.G

reec

e32

.70

(0.1

8)44

.Nor

way

1.77

44.U

rugu

ay0.

3945

.Con

go,R

ep.

32.8

2(0

.19)

45.V

anua

tu2.

1345

.Pap

uaN

ewG

uine

a0.

5046

.Ice

land

32.8

8(0

.20)

46.P

apua

New

Gui

nea

2.87

46.S

love

nia

0.59

47.G

erm

any

33.7

2(0

.28)

47.L

atvi

a3.

8547

.Cze

chR

ep.

1.11

48.N

icar

agua

34.0

9(0

.32)

48.S

riL

anka

3.93

48.P

ortu

gal

1.14

49.L

eban

on35

.18

(0.4

3)49

.Den

mar

k4.

1249

.Sou

thA

fric

a1.

4550

.Spa

in35

.22

(0.4

3)50

.Rom

ania

4.45

50.P

hilip

pine

s1.

58

200


51.N

amib

ia35

.43

(0.4

5)51

.Cze

chR

ep.

4.93

51.B

otsw

ana

1.74

52.J

amai

ca35

.44

(0.4

5)52

.Fin

land

4.97

52.F

inla

nd1.

8053

.Est

onia

35.5

1(0

.46)

53.A

ustr

ia5.

1853

.Ger

man

y2.

0954

.Mol

dova

35.7

2(0

.48)

54.E

ston

ia5.

4954

.Uni

ted

Kin

gdom

2.25

55.B

otsw

ana

35.9

8(0

.50)

55.U

nite

dK

ingd

om5.

5755

.Mal

ta2.

3356

.Cze

chR

ep.

36.2

1(0

.53)

56.A

lban

ia5.

5756

.Aus

tria

2.38

57.I

rela

nd36

.67

(0.5

7)57

.Leb

anon

5.74

57.N

amib

ia3.

3558

.Nor

way

38.9

3(0

.79)

58.B

otsw

ana

6.10

58.R

oman

ia3.

5059

.Mal

ta39

.06

(0.8

1)59

.Mal

ta6.

1359

.Jam

aica

4.69

60.L

uxem

bour

g39

.67

(0.8

7)60

.Jam

aica

6.59

60.L

eban

on4.

8961

.Slo

veni

a39

.92

(0.8

9)61

.Nam

ibia

6.70

61.S

riL

anka

4.99

62.P

olan

d40

.35

(0.9

3)62

.Slo

veni

a6.

7062

.Rus

sia

5.04

63.P

ortu

gal

40.8

1(0

.98)

63.P

ortu

gal

7.17

63.S

wed

en5.

5464

.Bul

gari

a40

.96

(0.9

9)64

.Con

go,R

ep.

7.18

64.B

ulga

ria

6.16

65.U

nite

dK

ingd

om41

.04

(1.0

0)65

.Fra

nce

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Why is the United States so poorly explained by this bivariate model?Why does this very rich country tax and spend at such low rates? Whilethere are many hypotheses, drawn from a rich and storied research tra-dition,24 I shall restrict myself here to the role of political institutions.Arguably, democratic institutions that centralize power, strengthen polit-ical parties, and condition an inclusive style of governance stimulate thegrowth of a welfare state.25 Hence, one ought to find larger welfarestates in countries with unitary (rather than federal) constitutions, list-proportional (rather than majoritarian or preferential-vote) electoral sys-tems, and parliamentary (rather than presidential) executives. In order totest these propositions across country-cases, one must code extant coun-tries on all three dimensions. Since these are complicated institutional fea-tures, with many admixtures, I employ the following three-point scalesfor each variable. UNITARISM: 1 = federal, 2 = semifederal, 3 = uni-tary. PR: 1 = majoritarian or preferential-vote, 2 = mixed electoral sys-tem, 3 = proportional. PARL: 1 = presidential, 2 = semipresidential,3 = parliamentary.26 With this information for each of the world’sseventy-seven democracies, one may then regress expenditure levels onGDP per capita plus these additional factors:

Expenditure = − 3.92 + 2.52GDPpc + 2.66Unitarism(E.2)

+ 1.19PR + 3.60Parl

R2 = .445 N = 77Residuals from this equation are presented in the third column ofTable E.1. The striking result is that the U.S. case has lost its outlier status.Indeed, it lies extremely close to the predicted value of the multivariatemodel.

One might conclude from this analysis that one has effectively “ex-plained” the American case. Of course, any such conclusion rests on lotsof assumptions pertaining to the veracity of the general model, the sta-tistical technique, possible measurement error, the homogeneity of thepopulation, and so forth. One can think of many different ways to modelthis problem, and one would probably want to make use of time-seriesdata in doing so. I have kept things simple with the goal of illustratingthe potential of nested analysis, when circumstances warrant.

Note that even if the model provides a good fit for the case ofspecial interest, as in equation E.2, there still may be strong reasons for

24 Marks and Lipset (2000).25 Huber and Stephens (2001); Huber, Ragin, and Stephens (1993); Swank (2002).26 Details on these coding procedures are explained in Gerring, Thacker, and Moreno

(2005b) and in Gerring and Thacker (forthcoming).



supplementing nested analysis with a more intensive analysis of thecase of special interest or of adjoining cases, as discussed in subsequentsections. However, in this circumstance the purpose of a researcher’scase-based analysis is likely to shift from (a) exogenous causal factors to(b) causal mechanisms. How might American political institutions havecontributed to the country’s welfare state trajectory? Are these the criticalcausal variables that the general model supposes (or are there reasons todoubt)?

If, on the other hand, a case is poorly explained by a general model (i.e.,when the residual is high), this also offers important clues for subsequentanalysis. Specifically, one has strong reason to presume that additionalfactors are at work – or, alternatively, that the outcome is a product ofpure chance (something that cannot be subjected to general explanation).

Regardless of how the evidence shakes out, one has presumably learneda good deal about the outcome of special interest – the American welfarestate – by exploiting available evidence from a large sample of adjacentcases. This is the purpose of nested analysis.

Most-Similar AnalysisWe have already discussed the most-similar method (see Chapter Five).It is no different in the context of a single-outcome analysis, with theexception that one of the most-similar cases is preselected. It follows thatthe chosen comparison case (or cases) should be that which is most similarto the case of special interest in all respects except the dimension(s) ofinterest to the researcher.

If the researcher has no hunch about the possible causes of Americanwelfare state development, then the search for a most-similar case involvesmatching the United States to another case that has a higher level ofgovernment expenditures and is fairly similar on various dimensions thatmight affect this outcome. Britain or Canada might fit the bill, since bothhave similar political cultures and larger welfare states. The research thenconsists of examining these cases closely to try to identify some contrastingfeature that might explain their different trajectories. This is most-similaranalysis in an exploratory format.

If the researcher has a hunch about why the United States has lowlevels of welfare spending, then the task of finding a paired comparison ismore determinate. In this situation, one searches for a country with higherlevels of welfare spending, a different status on the variable of interest,and similarities on all other factors that might affect the outcome. Let ussay that the researcher’s hypothesis concerns the constitutional separationbetween executive and legislature – the American doctrine of “separation



of powers.” In this circumstance, Canada might be the most appropriatechoice for a most-similar analysis, since that country has a parliamentaryexecutive but shares many other political, cultural, and social featureswith the United States.27

If an offhand survey of available cases is insufficient to identify a most-similar case – either because the number of potential candidates is largeand/or because the similarities and differences among them are not wellknown – the researcher may resort to truth tables (with comprehensivelistings of attributes) or matching techniques (see Chapter Five) as a wayof identifying appropriate cases.

Thus far, I have discussed the spatial components of most-similar com-parison – where variation across cases is essentially static (there is nochange, or at least no change of trend, in the variables of interest acrossthe chosen cases). This conforms to a Spatial Comparison, as discussedin Chapter Six. Wherever comparative cases embody longitudinal varia-tion, they offer an additional dimension for causal analysis. Indeed, thebest choice for most-similar analysis is a pairing that provides a DynamicComparison – replicating the virtues of a classic experiment (but with-out a manipulated intervention). Here, one can compare the outcome ofinterest before and after an intervention to see what effect it may havehad in that case – a sort of pre- and post-test. Unfortunately, for purposesof exploring the role of the separation of powers in U.S. welfare statedevelopment, there are no obvious comparison cases of this nature. Thatis, no countries that are reasonably well matched with the United Stateshave instituted constitutional changes in their executive (e.g., from pres-idential to parliamentary, or vice versa).28 Nor, for that matter, has theUnited States.

Within-Case AnalysisRegardless of how informative cross-case evidence (either large-N orsmall-N) might be, one is unlikely to be satisfied that one has satisfac-torily explained an outcome until one has explored within-case evidence.If there is a specific hypothesis that organizes the research, research designsmay be Dynamic, Spatial, Longitudinal, or Counterfactual (see Table 6.1).

27 The United States/Canada comparison is a fairly common one, though not all scholarsreach the same conclusions (e.g., Epstein 1964; Lipset 1990).

28 France adopted a semipresidential system in 1958. However, the primary locus oflegislative sovereignty still resides in parliament, so it is not a good test of thetheory.



Let us return to the previous hypothesis – the structure of the executive inconditioning a weak welfare state in the United States – to see how theseresearch designs might play out.

Since states within the union also pursue welfare policies, and sincetheir causal relationships may be similar to those that obtain at a nationallevel, one might exploit variation within and across states to illuminatecausal factors operative at the national level, where our ultimate theoreti-cal interest lies. Suppose that a state decides to abolish its executive office(the governor), creating what is, effectively, a parliamentary system atthe state level. Here is a terrific opportunity for a Dynamic Comparison.That state’s welfare levels can be measured before and after the interven-tion, and that state may also be compared to another state(s) that did notundergo constitutional change.

Suppose that at least one state in the union has always possessed aparliamentary system of government (from 1776 to the present). Underthis circumstance there is no intervention that can be studied, and nopre- and post-test may be administered. Still, one might compare levelsof spending in that state to those in similar states that have separate-powers constitutions in an attempt to judge the effects of constitutionalstructure on social policy and political development. This constitutes aSpatial Comparison.

A Longitudinal Comparison might be established at the national level.The American welfare state has been growing for some time, and whatevercausal dynamics are at work today have presumably been operative forsome time. Granted, there has never been a parliamentary executive in theUnited States, so there is no change on the variable of theoretical interest.However, there have been changes in the relative strength of the presidentand Congress, and this may offer some leverage on the question. Thereare also periods during which both branches have been controlled by thesame party, and periods of divided party control. These may be comparedaccording to the level of new legislation that they produce. This providesa picture of what the U.S. welfare state might look like today if all periodsof American history had been periods of single-party rule.29 To be sure,it may be doubted whether such brief periods of unified party controlapproximate the political circumstances of parliamentary systems; this is,at best, a poor substitute for a change in constitutional status, the actualvariable of interest.

29 Mayhew (1991).



Evidently, with this particular research question the opportunities forwithin-case empirical analysis are quite limited. As a consequence, theresearcher who wishes to apply a “parliamentary” explanation to theAmerican welfare state is likely to lean heavily upon Counterfactual Com-parison. What course would the American welfare state have taken if theUnited States possessed a parliamentary system? This is a difficult mat-ter to reconstruct. However, intelligent speculation on this point may behighly informative.30

The employment of counterfactual reasoning in the analysis of individ-ual outcomes is well established. Yet it also raises dicey questions of causallogic – for, in principle, virtually any event occurring prior to the outcomeand having some plausible causal connection to it might be invoked as anecessary antecedent cause. The laggard American welfare state might beattributed to the American Revolution, the Civil War, early democratiza-tion, weak and porous (and generally corrupt) bureaucracies, the failureof the Knights of Labor in the 1880s, Progressive-era reforms, World WarOne, the 1920s, the New Deal, the compromise between representativesof capital and labor after World War Two, the Cold War, and so forth.Each of these prior developments has been considered critical, by at leastsome historians, to the subsequent development (i.e., nondevelopment) ofthe American welfare state. And all of these arguments are more or lessplausible.

This is not an atypical situation, for most outcomes can be traced backto a wide variety of prior “turning points.” The causal regress is, in princi-ple, infinite, as is the number of possible counterfactual scenarios. (Whatif Gompers had failed to maintain control over the AFL? What if busi-nesses had not been so hostile to the organization of labor unions in theinterwar period?) Recall that in a generalizing case study, one’s consid-eration of causal factors is limited to those that might plausibly explainvariation across a broader population of cases. But no such restrictionapplies to single-outcome studies. Consequently, this genre of endeavoris rather intractable, for the outcome is radically overdetermined. Thereare too many possible – and probable – causes. The options are, quiteliterally, infinite.

Mitigating this problem is a special restriction that applies to the coun-terfactual analysis of individual outcomes. Philosophers and social scien-tists have come to agree that the most sensible counterfactual within a field

30 See, e.g., Sundquist (1992).



of possible counterfactuals is that which demands the smallest alterationin the course of actual events, as they really did happen. This principleof causal reconstruction has come to be known as the minimal-rewriterule.31 The author should play God with history with as light a hand aspossible. All other things being equal, when deciding between two expla-nations of a given outcome the researcher should choose the cause that ismost contingent. It is the turning point, the critical juncture, that rightlydeserves the label “cause” – not the factors that probably could not havebeen otherwise. The effect of this criterion is to eliminate absurd conjec-tures about the course of history. One might suppose, for example, thatthe American welfare state would have developed differently if Europeanshad never discovered America. While perhaps true, this counterfactual isnot a very useful reconstruction of history because it envisions a scenariothat departs radically from the actual course of events. Of course, theminimal-rewrite rule will not discriminate among all the hypotheses thatmight be generated through the counterfactual analysis of a single out-come. But, at least it will narrow the field.32

Putting Cross-Case and Within-Case Evidence Together

Having reviewed three fundamental methods of single-outcome analysis –nested analysis, most-similar analysis, and within-case analysis – the easyconclusion is that all three of these methods ought to be employed, wher-ever possible. We gain leverage on a causal question by framing theresearch design in different ways and evaluating the evidence drawn fromthose separate and independent analyses. To the extent that a particularexplanation of an outcome is confirmed by nested analysis, most-similaranalysis, and within-case analysis, one has successfully triangulated.

However, it is not always possible to employ all three methods. Or,to put it more delicately, these three methods are not always equally

31 Bunzl (2004); Cowley (2001); Einhorn and Hogarth (1986); Elster (1978); Fearon (1991);Hart and Honore (1959: 32–3; 1966: 225); Hawthorn (1991); Holland (1986); Mackie(1965/1993: 39); Marini and Singer (1988: 353); Taylor (1970: 53); Tetlock and Belkin(1996: 23–5); Weber (1905/1949). Also known as “cotenability” (Goodman 1947) and“compossibility” (Elster 1978).

32 Note that the minimal-rewrite rule has the additional effect of nudging single-event anal-ysis away from general, structural causes and toward unique, proximate causes, whichare (almost by definition) more contingent. Compare two classic explanations of Amer-ican exceptionalism: (a) the great frontier (Turner 1893/1972) and (b) the failure of theKnights of Labor in the 1880s (Voss 1993). Evidently, the second event is more likely tohave turned out differently than the first.



viable. And even when all three are possible and viable, sometimes theconclusions reached are inconsistent. For example, cross-case evidencemay suggest one causal factor and within-case analysis another. The threemethods reviewed here might even suggest three different causal factors.

This sort of dissonance is mildly problematic in the generalizing casestudy, where the purpose of the investigation is to shed light on cross-case causal relationships. Here, one can reasonably dismiss idiosyncraticfindings drawn from a single case as “noise” – stochastic variation orvariation that for some reason remains unexplained. In single-outcomestudies, however, the purpose of the study is to explain that particular case.Here, varying results from cross-case and within-case analyses cannot betreated lightly. And here, because the objective is to provide a reasonablycomplete explanation, it is not permissible to dismiss evidence as part ofthe error term (noise).

Complicating matters further, certain hypotheses garnered fromwithin-case analysis may be effectively untestable in a cross-case setting.Consider the following arguments that the research team of Acemoglu,Johnson, and Robinson provide to explain Botswana’s good policies andinstitutions and, from thence, its extraordinary economic success in thepost-independence era.

1. Botswana possessed precolonial tribal institutions that encouraged broad-basedparticipation and placed constraints on political elites. 2. British colonization hada limited effect on these precolonial institutions because of the peripheral natureof Botswana to the British Empire. 3. Upon independence, the most importantrural interests, chiefs and cattle owners, were politically powerful, and it was intheir economic interest to enforce property rights. 4. The revenues from diamondsgenerated enough rents for the main political actors, increasing the opportunitycost of, and discouraging, further rent seeking. 5. Finally, the post-independencepolitical leaders, in particular Seretse Khama and Quett Masire, made a numberof sensible decisions.33

All these factors are adduced to help explain why Botswana adoptedgood (market-augmenting) policies and institutions. But few are easilytested across a wide range of country-cases. Does the existence of certainTswana-like tribal institutions lead to broad-based political participationand constrained elites in other polities? Does “light” imperial control leadto better post-independence politics? Is it advantageous for rural intereststo dominate a country politically? Each of these statements, if generalizedto include a broad set of country-cases, is questionable. But few are easy to

33 Acemoglu, Johnson, and Robinson (2003: 113).



test. The final argument, having to do with leadership, is true everywherealmost by definition (good leadership is usually understood as leadershipthat leads to good policy outcomes), and therefore does not tell us verymuch. To be sure, the authors present these five arguments as conjointcauses; perhaps all must be present in order for salubrious results to ensue.If so, then the argument is virtually incapable of broader application. Thismeans that we must accept the authors’ claims based largely on within-case evidence (plus a smattering of two-case comparisons that addressdifferent elements of the story).

It is quite common in single-outcome analysis to rest an inference or aset of inferences upon evidence drawn from that case alone, and there isnothing in principle wrong with this style of argumentation. Nonetheless,Acemoglu, Johnson, and Robinson would be able to make a stronger andmore convincing argument if they could show more cross-case evidencefor their various propositions. In a few instances, statements made withreference to Botswana seem to fly in the face of other countries’ historicalexperiences. For example, while the authors attribute Botswana’s successto its light-handed, noninterventionist colonial history, it seems likely thatgrowth rates in countries around the world are positively correlated withthe length and intensity of colonial control – particularly if the colonialpower is British, as it was in Botswana.34 It is possible, of course, thatthe effect of a rather crude variable like colonialism is not uniform acrossall countries. Indeed, there is no reason that we should accept uncriticallythe results of a cross-country regression that tells this particular story. Butwe have no cause to dismiss it either.

The point of this discussion is not to argue for or against any particularstyle of evidence but rather to point to a vexing methodological problemthat affects virtually all single-outcome analysis. Cross-case and within-case evidence often tell somewhat different stories, and there is usuallyno easy way to adjudicate between them. About all that one can say isthat the strength of each sort of evidence rests upon the particulars of theevidence. Thus, if the cross-case analysis is sketchy – if, for example,the author is suspicious of how key variables have been operationalized,the specification of the model, or the robustness of the results – then shemay choose to place less emphasis on these results. Likewise, if the within-case evidence is sketchy – if, for example, the case might be reconstructedin a variety of different ways, each of which provides a plausible fit for

34 Grier (1999); La Porta et al. (1999).



the theory and the evidence – then she may choose to place less emphasison these results. In short, it all depends.

Conclusion

At this juncture, the reader may have come to the conclusion that single-outcome analysis is singularly difficult, and case study analysis corre-spondingly easy. This is not the message I wish to convey. Indeed, I indi-cated at the outset of this chapter that single-outcome arguments are oftenless uncertain than the corresponding cross-case arguments (for which thecase study might be employed as a mode of analysis). A murder may beeasier to solve than general problems related to criminal activity.

However, the sort of single-outcome studies that social scientists focuson explaining are also typically the sort that are difficult to parse. And this,in turn, rests upon their singularity. It is the unusualness of the outcome,not the method applied to the single-outcome study, that makes thesestudies so recalcitrant. The American welfare state will never have a con-clusive explanation. The United States is too different from other nations,and there are too few other nations, to allow for this degree of certainty.The same might be said about World War One and the French Revolution.The more unique an outcome the more difficult it is to explain, becausewe have fewer comparison cases, and the few cases that do present them-selves suffer problems of causal comparability. With crimes it is different.This is why judges and juries charged with rendering verdicts generallyshow greater confidence in their judgments than academics charged withexplaining crime (in general).

But academics do not write case studies of individual crimes – unless,of course, those cases are sufficiently unusual to warrant individual treat-ment (e.g., crimes with immense political repercussions, such as the Water-gate burglary). Again, one finds that the single-outcome study is problem-atic not by reason of any inherent methodological difficulty but ratherby virtue of the situations in which it is typically deployed. There islittle need for single-outcome studies of typical outcomes. Consequently,single-outcome studies tend to be singular-outcome studies. In sum, it isthe choice of topic – not the method – that renders this genre problematic.

P1: JZP052185928Xapxa CUNY472B/Gerring 0 521 85928 X Printer: cupusbw October 5, 2006 11:15

Glossary

This glossary was constructed in consultation with other glossaries, includingSchwandt (1997), Seawright and Collier (2004), and Vogt (1993). Italicized wordsare found elsewhere in the glossary. (Very common words such as “case” aretypically not italicized.)

Antecedent cause See causal order.Attribute An aspect of a topic or, more specifically, of an observation. Synonyms:dimension, property, characteristic. May be measured by a variable.Bias Characterizes a sample that is not representative of a population, with re-spect to some inference. Contrast: representativeness. (In statistical parlance, biasrefers to the properties of multiple samples drawn from the same population. Thisis similar, but not identical, to my usage in the text.)Binary See level of measurement.Breadth See population.Case A spatially and temporally delimited phenomenon observed at a singlepoint in time or over some period of time – for example, a political or socialgroup, institution, or event. A case lies at the same level of analysis as the principalinference. Thus, if an inference pertains to the behavior of nation-states, casesin that study will be comprised of nation-states. An individual case may also bebroken down into one or more observations, sometimes referred to as within-caseobservations. Compare: case study.Case-based analysis A variety of analyses that focus on a small number of rela-tively bounded units. May refer to case studies, single-outcome studies, or – moretenuously – Qualitative Comparative Analysis (QCA).Case selection The identification of cases chosen for analysis in a study. The first,and perhaps most important, component of case study research design.Case study The intensive study of a single case for the purpose of understand-ing a larger class of similar units (a population of cases). Synonyms: single-unitstudy, single-case study, within-case study. Note that while “case study” issingular – focusing on a single unit – a case study research design may refer to

211


212 Glossary

a work that includes several case studies (e.g., comparative-historical analysis orthe comparative method). Contrast: single-outcome study and cross-case study.Causal effect The impact of an explanatory factor on an outcome. Understoodas the change in Y corresponding to a given change in X. Applicable either to aparticular case or across a set of cases (averaged).Causal distance A distal (or structural) cause lies far from the effect it is intendedto explain. A promixal (or proximate) cause lies close to the effect it is intendedto explain. Causal mechanisms are generally composed of proximal causes; theyare, in any case, more proximal than the structural cause they are enlisted to helpexplain.Causal factor See independent variable.Causal inference A causal relationship is one where – minimally – a causal factor(X) may be said to raise the probability of an effect occurring (Y). Contrast:descriptive inference. See Gerring (2005).Causal mechanism That which explains a covariational relationship betweenX and Y. The causal pathway, or connecting thread, between X and Y, usuallyembodied in a theory or model. See causal order.Causal order A causal argument may be conceptualized as consisting of a struc-tural (a.k.a. antecedent, exogenous) cause (X1), an intermediate cause (X1a), andan outcome (Y). The intermediate cause(s) performs the role of a causal mecha-nism, a pathway from X1 to Y.Ceteris paribus All other things being equal. In the context of research design, thismeans that whatever variation is being exploited for the purpose of investigatingcausal relationships is the product of the causal factor of interest (X1) and notof other confounding factors (X2). If the researcher is comparing a case beforeand after an intervention to see what effects the intervention might have had onsome outcome (Y), she must assume that the case remains similar, pre- and post-intervention, in all other respects that might affect Y (and cannot be attributed toX1). If the researcher is comparing two cases that differ in their properties on acausal factor of interest (X1), she must assume that they are the same on all otherdimensions (X2) that might affect Y.Comparative method Causal analysis focused on a small number of regionsor states where spatial variation assumes a most-similar format. There may, ormay not, be temporal variation encompassing the causal factor(s) of interest. SeeCollier (1993).Comparative-historical analysis Causal analysis focused on a small number ofregions or states where spatial variation assumes a most-similar format and tem-poral variation includes the causal factor(s) of special interest. A species of thecomparative method in which spatial and temporal variation are combined in asingle study. See Mahoney and Rueschemeyer (2003).Continuous (scalar) variable See level of measurement.Correlation See covariation.Counterfactual comparison See experimental template.Counterfactual thought experiment An attempt to replay the events in a par-ticular case history in order to determine what the result might have been undera different set of circumstances. An essential tool of causal analysis when the


Glossary 213

possibilities of real (observable) variation are meager or where the outcome ofinterest lies in the past (and cannot be effectively re-created).Covariation The association of two factors (variables), said to covary. Covari-ational patterns may be diachronic (a.k.a. temporal, time-series, longitudinal,historical), synchronic (a.k.a. spatial, cross-sectional), or both. Covariation maybe located at different levels of analysis. Synonyms: correlation, association.Critical juncture/path dependence A critical juncture refers to the contingentmoment in a longer trajectory. It is followed by a period of path dependencein which a given trajectory is maintained, and perhaps reinforced (“increasingreturns”).Cross-case study Refers in this text to a large-sample study where the sampleconsists of multiple cases (representing the same units that comprise the centralinference), analyzed statistically. Contrast: case study.Cross-sectional See covariation.Crucial case A case that offers particularly compelling evidence for, or against, aproposition. Synonym: critical case. Assumes two varieties: least-likely and most-likely. A least-likely case is one that is very unlikely to validate the predictions ofa model or a hypothesis. If a least-likely case is found to be valid, this may beregarded as strong confirmatory evidence. A most-likely case is one that is verylikely to validate the predictions of a model or a hypothesis. If a most-likely caseis found to be invalid, this may be regarded as strong disconfirming evidence.Dependent variable See variable.Descriptive inference Answers questions about who, what, when, and how. Mayinclude proximate causes. Contrast: causal inference.Deterministic An invariant causal relationship; there are no random (stochastic)components. Usually, deterministic arguments take the shape of necessary, suffi-cient, or necessary-and-sufficient causal relationships. Contrast: probabilistic.Deviant case A case exemplifying deviant values according to some generalmodel.Diachronic See covariation.Dichotomous scale See level of measurement.Distal cause See causal distance.Diverse case A case exemplifying diverse values along relevant dimensions (X1,Y, or X1/Y). Uses: to illuminate (a) the full range of variation on X1 or Y (anopen-ended probe), or (b) the various causal pathways or causal types exhibitedby X1/Y (a more determinate hypothesis).Domain See population.Dynamic comparison See experimental template.Endogenous cause See causal order.Equifinality Multiple causal paths leading to the same outcome.Ethnography Work conducted “in the field,” that is, in some naturalistic settingwhere the researcher observes her topic. Near-synonyms: field research, partici-pant observation.Exogenous cause See causal order.Experimental research design A design where the causal factor of interest (thetreatment) is manipulated by the researcher. May also incorporate a randomizedcontrol group. Contrast: observational research design.


214 Glossary

Experimental template Classic experimental research designs achieve variationthrough time and across space, thus maximizing leverage on the fundamentalproblem of causal inference. When this template is adopted for use in case studyresearch, the latter may be understood as part of a matrix with four cells (see Figure6.1). The Dynamic Comparison mirrors the paradigmatic laboratory experiment,since it exploits temporal and spatial variation. The Longitudinal Comparisonemploys only temporal variation and is similar in design to the experiment withoutcontrol. The Spatial Comparison employs only spatial variation; it purports tomeasure the outcome of interventions that occurred at some point in the past(but that are not directly observable). The Counterfactual Comparison relies onvariation (temporal and/or spatial) that is imaginary.External validity See validity.Extreme case A case exemplifying unusual values on X1 or Y relative to someunivariate distribution (measured or assumed).Falsifiability The possibility that a theory or hypothesis may be proven wrong.A nonfalsifiable hypothesis is one that cannot be disproven by appeal to empiricalevidence.Field research See ethnography.Hermeneutics See interpretivism.Hypothesis A specific, and hence falsifiable, supposition. A causal hypothesissuggests a specific X1/Y relationship across a (more or less) defined populationof cases – for example, “Proportional representation electoral systems moderateethnic conflict (in all democratic polities where substantial ethnic heterogeneityis present).” A hypothesis may be connected to a larger theory or theoreticalframework (a.k.a. paradigm), or it may stand alone. Near-synonyms: argument,inference, proposition, thesis.Independent variable See variable.Inference See hypothesis.Influential case A case with a configuration of scores on various independentvariables that strongly influences a general cross-case model of causal relations,and which therefore may merit close attention (i.e., case study analysis).Intermediate cause See causal mechanism and causal order.Internal validity See validity.Interpretivism Broadly, the study of human meanings and intentions. More nar-rowly, the attempt to interpret human behavior in terms of the meanings assignedto it by the actors themselves. Near-synonyms: hermeneutics, Verstehen.Intervention Any change in a key causal variable that can be observed throughtime, whether experimental (a manipulated treatment) or observational (a naturaltreatment).K The total number of variables in an analysis.Large-N See observation.Least-likely case See crucial case.Level of analysis The level of aggregation at which an analysis takes place. If ahypothesis is concerned primarily with the behavior of nation-states, then lowerlevels of analysis would include individuals, institutions, and other actors at asubstate level. Usually, case study work incorporates evidence at a lower level


Glossary 215

of analysis than the proposition of primary interest, thus providing within-caseobservations.Level of measurement Measurements (scales) may be dichotomous (a.k.a. binary,e.g., 0/1), nominal (e.g., yellow, red, green), ordinal (e.g., strongly agree, agree, nei-ther agree nor disagree, disagree, strongly disagree), interval (e.g., degrees Fahren-heit), or ratio (an interval scale with a true zero, e.g., degrees Kelvin). Dichoto-mous, nominal, and ordinal scales are all categorical. Interval and ratio scales arecontinuous.Longitudinal comparison See experimental template.Method of difference See most-similar cases.Minimal-rewrite rule In a single-outcome study, there are always multiple poten-tial factors that may be invoked as “causes.” From among these potential expla-nations, the most useful counterfactual is that which requires the least alterationin the course of actual events. The researcher should focus on the most contingentcause, not on more or less permanent features of the landscape.Most-different cases Cases are different in all respects except the variables oftheoretical interest (X1 and Y). Synonym: method of agreement (J. S. Mill).Most-similar cases Cases are similar in all respects except the variables oftheoretical interest (X1, Y, or X1/Y). Synonym: Method of difference (J. S.Mill).N See observation.Naturalistic Research settings that are, or resemble, “real-life” settings. Unob-trusive methods of research. Contrast with laboratory experiments and otherartificial settings.Natural experiment See quasi-experiment.Necessary cause See deterministic.Nested analysis Understood in this text as the employment of a large-N cross-case analysis in order to shed light on a single outcome. Used in the context of asingle-outcome study. Near-synonym: nested inference.Nominal scale See level of measurement.Noncomparable observations Observations that are not comparable (non–unithomogenous) to one another.Observation The most basic element of any empirical endeavor. Any piece ofevidence enlisted to support a proposition. Conventionally, the number of obser-vations in an analysis is referred to by the letter N. (Confusingly, N is also usedto refer to the number of cases.) If observations are comparable they may berepresented as rows in a rectangular dataset.Observational research design A design where the causal factor of interest is notmanipulated by the researcher. Contrast: experimental research design.Operationalization Formulation of a concept in terms of measurable indicators,or of a general theory in terms of testable hypotheses. The issue of operational-ization is the issue of measurement – that is, how do I know concept A or theoryB when I see it?Ordinal scale See level of measurement.Participant observation Ethnographic work in which the researcher is a partic-ipant in the activity under study.Path dependence See critical juncture/path dependence.


216 Glossary

Pathway case A case that embodies a distinct causal path from X1 to Y such thatpotential confounders (X2) are isolated from the analysis and the true relationshipbetween X1 and Y can be more easily observed. Useful for the identification ofcausal mechanisms.Population The universe of cases and observations to which an inference refers.Usually, much larger than the sample under investigation. Synonyms: breadth,domain, scope.Probabilistic A model or process – specifically, a causal relationship – with ran-dom (stochastic) properties. In a statistical model, these are captured by the errorterm.Process tracing A style of analysis used to reconstruct a causal process that hasoccurred within a single case. (Because the event of interest has occurred in thepast, this sort of analysis generally cannot employ a manipulated treatment.) Itsdefining features are that (a) multiple types of evidence (noncomparable obser-vations) are employed for the verification of a single causal outcome and (b) thecausal process itself is usually quite complex, involving a long causal chain andperhaps multiple switches, feedback loops, and the like.Proposition See hypothesis.Proximal (proximate) cause See causal distance.Qualitative Having few observations (small-N), and hence analyzed with wordsrather than numbers. (Another, unrelated meaning of qualitative refers specifi-cally to variables, specifically those that are categorical rather than continuous.)Contrast: quantitative.Qualitative Comparative Analysis (QCA) A method of analyzing causal rela-tionships associated with the work of its inventor, Charles Ragin, that is sensitiveto necessary and sufficient relationships, conjunctural causes, and causal equi-finality, but which also manages to incorporate a large number of cases. Laterversions of QCA, abbreviated “fs/QCA,” incorporate elements of probabilismand fuzzy-set theory.Quantitative Having many observations (large-N). Analyzed with numbers(statistically) rather than words. Contrast: qualitative.Quasi-experiment An observational study that nonetheless has the properties ofan experimental research design. Synonym: natural experiment.Randomization A process by which cases in a sample are chosen randomly(with respect to some subject of interest). An essential element for experimentsthat use control groups, since the treatment of control groups must be similar (inall respects relevant to the inference), and the easiest way to achieve this is throughrandom selection. Not recommended for case study analysis.Representativeness A sample is representative when its cases (and observations)are similar (i.e., comparable, unit homogeneous) to a broader population in allrespects that might affect the causal relationship of interest. Synonym: typical.Antonym: bias.Research design Generally, the way in which empirical evidence is brought tobear on a hypothesis. Includes case selection and case analysis.Sample The set of cases (and observations) upon which the researcher isfocused. Assumed to be representative of some population, which is usually largerthan the sample. A case study focused on a single case comprises a sample ofone, though the term is rarely used in this context.


Glossary 217

Scope See population.Selection bias A form of bias that is introduced whenever the treatment (thecausal factor of interest) is not randomly assigned across cases, thus violating theceteris paribus assumption of causal analysis.Single-outcome study Seeks to explain a single outcome occurring within a singlecase. Near-synonyms: particularizing case study, idiographic case study. Contrast:case study.Small-N See observation.Spatial Comparison See experimental template.Stochastic See probabilistic.Structural cause See causal order.Sufficient cause See deterministic.Synchronic See covariation.Triangulation The use of multiple methods, often at different levels of analysis.Typical case A case exemplifying a typical value according to some model. Sta-tistical measure: a low-residual case (on-lier). Uses: to probe causal mechanisms.Unit In most situations, equivalent to a case. Pertains to the spatial (not thetemporal) components of a case.Unit of analysis The species of observations that will be analyzed in a particularresearch design. If the design is synchronic, then the unit of analysis is spatial(e.g., nations or individuals). If the design is diachronic, then the unit of analysisis temporal (e.g., decades, years, minutes). If the design is both synchronic anddiachronic, then the unit of analysis has both spatial and temporal components(e.g., country-years). Evidently, the unit of analysis may change in the course ofa given study. Even so, within the context of a particular research design it mustremain constant.Unit homogeneity The comparability of cases or observations in all respects thatmight affect a particular causal relationship. Near-synonyms: causal homogeneity,equivalence.Validity Internal validity refers to the correctness of a hypothesis with respectto the sample (the cases actually studied by the researcher). External validityrefers to the correctness of a hypothesis with respect to the population of aninference (cases not studied). The key element of external validity thus rests uponthe representativeness of the sample.Variable An attribute of an observation or a set of observations. Depicted asvertical columns in a rectangular dataset. In the analysis of causal relations, vari-ables are understood either as independent (a.k.a. explanatory or exogenous),denoted X, or as dependent (endogenous), denoted Y. In this text, X1 refers to theindependent variable of theoretical interest (if any), and X2 refers to the vector ofcontrol variables (variables that might affect Y but are not of central theoreticalconcern). Note that my usage of the term variable is quite general and does notpresume statistical analysis.Verstehen See interpretivism.Within-case study Analysis of observations within a single case. May be small-Nor large-N. Contrast: cross-case study.X See variable.X-centered analysis Exploratory research where the puzzle or question concernsa particular causal factor (X1) but no specific outcome (Y).


218 Glossary

X1/Y–centered analysis Confirmatory research into a specific, falsifiable causalhypothesis – the posited relationship between X1 (a particular causal factor) andY (the outcome).Y See variable.Y-centered analysis Exploratory research where the puzzle or question concernsa particular outcome (Y) but (at least initially) no particular causal factor (X1).

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Name Index

Abadie, Alberto, 2, 159, 160Abbott, Andrew, 3, 4, 11, 50, 61, 100Abell, Peter, 3, 4Abrami, Regina M., 70Acemoglu, Daron, 2, 191, 208–10Achen, Christopher H., 3, 6, 13, 31, 44,

46, 145, 157Adcock, Robert, 15Alesina, Alberto, 48, 159Alexander, Jeffrey, 1Allen, William Sheridan, 120Allison, David B., 2, 18, 19, 160, 162Allison, Graham T., 76Almond, Gabriel A., 54, 120Alperovitz, Gar, 191Alston, Lee, 2Amenta, Edwin, 22, 106Anderson, Terry L., 194Angrist, Joshua D., 44Anscombe, G. E. M., 70Athens, Lonnie H., 69Atkinson, Paul, 69

Bailey, Mary Timney, 2Baker, Rigina M., 3Banerjee, Abhijit V., 165–7, 168Barlow, David H., 2, 6, 7, 18, 19, 30, 51,

91, 162Barresi, Paul A., 19, 37Barrett, Christopher B., 69Barro, Robert J., 127Bartels, Larry M., 3Barton, Allen H., 99Bates, Robert H., 2, 5, 78. 197Baur, Martin, 75, 164Beasley, Ryan K., 2Becker, Howard S., 2, 69, 71

Belkin, Aaron, 4, 166, 207Belsey, David, 110Belwood, Marily F., 161Benbasat, Izak, 2, 19Bendix, Reinhard, 3, 50Bennett, Andrew, 2, 4, 5, 17, 44, 61, 69,

75, 76, 81, 98, 99, 115–18, 145, 173,181, 193

Bentley, Arthur, 54, 120Berelson, Bernard, 34Berg-Schlosser, Dirk, 13Bernard, Luther Lee, 85Bernhard, H. Russell, 2Bevan, David, 2Bhagwati, Jagdish N., 2Bhaskar, Roy, 5Bloch, Marc, 69Blumer, Herbert, 50Bobo, Lawrence, 157Bock, Edwin A., 2Boix, Carles, 95Bollen, Kenneth A., 3Bonoma, Thomas V., 2, 39Bosk, Charles L., 69Bound, John, 3Brady, Henry E., 2, 4, 158, 173, 174, 176,

178, 179, 183Braumoeller, Bear F., 4, 122, 123–6Breman, Anna, 145Brenner, Robert, 132Brooke, Michael Z., 11, 31Brown, Christine, 2Brown, James Robert, 166Brown, Michael E., 195Browne, Angela, 101Bryce, James, 27Buchbinder, Susan, 105

257


258 Name Index

Bueno de Mesquita, Bruce, 5Bunge, Mario, 5Bunzl, Martin, 207Burawoy, Michael, 2, 69Burgess, Ernest W., 69Burman, Erica, 69Burton, Alice, 69Buthe, Tim, 4

Caldeira, Gregory A., 160Cameron, David, 48Campbell, Angus, 34Campbell, Donald T., 2, 11, 17, 29, 40–2,

80, 157, 158, 169, 170Campoy, Renee, 2Canon, David T., 47Card, David, 158Cason, Jeffrey W., 69Chandra, Kanchan, 2Chang, Eric C.C., 2Chatfield, Chris, 3Chernoff, Brian, 2Chong, Dennis, 45Coase, Ronald H., 2Cochran, William G., 99Cohen, Morris R., 131, 142Colby, Anne, 69Coleman, James S., 30, 110Collier, David, 2, 4, 15, 27, 54, 75, 80, 81,

99, 101, 109, 110, 120, 139, 142, 145,173, 211

Collier, Paul, 2Collier, Ruth Berins, 75, 139, 142Colomer, Josep M., 123Converse, Philip E., 139Cook, Thomas D., 11, 157Coppedge, Michael J., 106, 198Cornell, Svante E., 158, 159Corsini, Raymond J., 2, 19Costello, Charles G., 18, 19, 160Coulthard, Malcolm, 69Cowley, Robert, 166, 207Cunningham, J. Barton, 19

Danto, Arthur C., 173Davidson, Donald, 2, 70, 192Davidson, Patrick Olof, 18, 19, 160De Meur, Gisele, 13Defelice, E. Gene, 139, 142Denzin, Norman K., 69Desch, Michael C., 115Dessler, David, 5, 44Devereaux, Charan, 2Deyo, Frederic, 101Dillman, Don A., 69Dion, Douglas, 104, 120Diprete, Thomas A., 3

Drass, Kriss, 4Dufour, Stephane, 2Dupeux, Georges, 139

Eaton, Kent, 75Ebbinghaus, Bernhard, 3Eckstein, Harry, 2, 11, 17, 41–3, 48, 50,

75, 76, 106, 115–17, 118, 120, 121Efron, Bradley, 11Eggan, Fred, 131Eichengreen, Barry, 177Einhorn, Hillel J., 207Elman, Colin, 4, 99, 106Elman, Miriam, 75Elster, Jon, 5, 44, 166, 207Elton, Geoffrey R., 69Emerson, Robert M., 69Emigh, Rebecca, 102, 106Epstein, Leon D., 132, 133, 138, 139, 204,

213Erikson, Robert, 77Ertman, Thomas, 109Esping-Andersen, Gosta, 100Estroff, Sue E., 69

Fauci, Anthony S., 105Feagin, Joe R., 2, 17, 42–50, 66Fearon, James D., 4, 166, 207Fechner, Gustav Theodor, 29, 30Feng, Yi, 48Fenno, Richard F., Jr., 69, 72, 179Ferejohn, John, 70Fisher, Ronald Aylmer, 157Fisman, Raymond, 2Flyvbjerg, Bent, 37, 150Fogel, Robert W., 182Forrest, John, 4, 100Fortin, Dominic, 2Foster, Peter, 2Franklin, Ronald D., 2, 18, 19, 160, 162Freedman, David A., 3, 11–13Freeman, John, 5, 11, 197Friedman, Milton, 5, 163

Gadamer, Hans-Georg, 70Gamson, Joshua, 69Gangl, Marcus, 3Gardeazabal, Javier, 2, 159, 160Garfinkel, Harold, 69Gaudet, Hazel, 34Geddes, Barbara, 6, 31, 40, 80, 101, 105,

145Geertz, Clifford, 70, 75, 104George, Alexander L., 2, 4, 5, 17, 44, 46,

47, 51, 61–2, 69, 75, 76, 78, 80, 81, 98,99, 115–18, 145, 173, 181

Gerber, Alan S., 11, 158


Name Index 259

Gerlagh, Reyer, 48Gerring, John, 9, 15, 19, 37, 39, 44, 75,

95, 131, 139, 142, 145, 149, 164, 202Gibbons, Michael T., 70Gibson, James L., 160Giddings, Franklin Henry, 29Gill, Christopher J., 181Gill, Jeff, 3Glaeser, Edward, 48Glaser, Barney G., 45Glaser, James, 157Glennan, Stuart S., 5Goertz, Gary, 4, 102, 120, 189, 191Golden, Miriam A., 2Goldstein, David K., 2, 19Goldstone, Jack A., 4, 45, 76, 173Goldthorpe, John H., 6, 31, 61, 76–7, 81,

190Gomm, Roger, 2, 17Goode, William J., 17Goodin, Robert E., 115Goodman, Nelson, 207Gordon, Sanford C., 85Gorman, Bernard S., 2, 18, 19, 160, 162Gosnell, Harold F., 157Green, Donald P., 11–13, 81, 82Greene, William H., 95, 158Greif, Avner, 78Grier, Robin M., 78, 209Griffin, Larry J., 4Gubrium, Jaber F., 69Gujarati, Damodar N., 91Gunning, Jan Willem, 2Gutting, Gary, 53

Hahn, Jinyong, 134Hall, Peter A., 4, 53, 173Hamel, Jacques, 2, 17, 69Hamilton, Gary G., 132Hammersley, Martyn, 2, 17, 69Harding, David J., 134Hardy, Cynthia, 69Harre, Rom, 5Hart, H. L. A., 189, 207Hart, Paul K., 17Hart, Roderick P., 2Hawthorne, Geoffrey, 207Haynes, Barton F., 105Hedstrom, Peter, 5, 44Heidbreder, Edna, 162Helper, Susan, 69Hempel, Carl G., 5, 117Herrera, Yoshiko M., 4Hersen, Michel, 2, 7, 18, 19, 29, 30, 51,

91, 157Heston, Alan, 95Hicks, Alexander, 4

Hill, Peter J., 183Hirano, Keisuke, 134Hirsch, E. D., 70Hirschman, Albert O., 70Ho, Daniel E., 134Hochschild, Jennifer L., 45Hogarth, Robin M., 207Holland, Paul W., 207Holstein, James A., 69Honore, A. M., 189, 207Houser, Daniel, 11, 197Howard, Marc Morje, 69, 140, 141, 142,

143, 144Howson, Colin, 114–17Hoy, David Couzens, 70Hsieh, Chang-Tai, 177, 178, 179, 183, 191Huber, Evelyne, 202Huber, John D., 2Hull, Adrian Prentice, 2Humphreys, Macartan, 127, 128

Imai, Kosuke, 134Imbens, Guido W., 134Iyer, Lakshmi, 165–68

Jackman, Robert W., 3Jackman, Simon, 95Jaeger, David A., 3Jaggers, Keith, 95Janoski, Thomas, 4Jenicek, Milos, 105Jensen, Jason L., 2Jervis, Robert, 46Jessor, Richard, 69Johnson, Simon, 2, 191, 208–10

Kaarbo, Juliet, 2Kadzin, Alan E., 18Kagel, John H., 157Kapur, Devesh, 4Karl, Terry Lynn, 139, 142Katz, Jack, 69Kaufman, Herbert, 179, 211Kazancigil, Ali, 105Kazdin, Alan E., 162Keen, Justin, 2Kemp, Kathleen, 115Kendall, Patricia L., 106Kennedy, Craig H., 2Kennedy, Peter, 44, 91Keohane, Robert O., 6, 9, 31, 39, 40, 61,

80, 145, 166, 190Khong, Yuen Foong, 119Kinder, Donald, 157, 160, 162King, Charles, 31King, Gary, 3, 6, 9, 11, 39, 40, 61, 80, 104,

145, 166, 190


260 Name Index

Kittel, Bernhard, 3, 4, 55Kornblum, William, 69Kratochwill, Thomas R., 6, 18Krippendorff, Klaus, 69Kritzer, Herbert M., 68Kroger, L. A., 69Krueger, Alan B., 44, 158Kuh, Edwin, 110Kuhn, Thomas S., 53

Lakatos, Imre, 106Lancaster, Thomas D., 164Lane, Robert, 34, 35, 43La Porta, Rafael, 209Lasswell, Harold, 27Laver, Michael, 69Lawrence, Robert Z., 2Lazarsfeld, Paul F., 6, 34, 99Le Play, Frederic, 2, 11, 31Leamer, Edward E., 3Lebow, Richard Ned, 4, 166, 196Lecroy, Craig Winston, 2Lee, Allen S., 11Lepgold, Joseph, 115Leplin, Jarrett, 5Levi, Margaret, 5, 37, 78, 116–19Levine, Ross, 55Levy, Jack S., 4, 115, 123, 189, 190, 191Libecap, Gary, 2Lieberman, Evan S., 69, 156, 198Lieberson, Stanley, 6, 13, 31, 61, 190Lijphart, Arend, 2, 6, 17, 27, 54, 75, 120,

131, 139Lincoln, Yvonna S., 69Lipset, Seymour Martin, 30, 54, 95, 109,

110, 120, 132, 202, 204Lipsey, Mark W., 26Little, Daniel, 5, 173Lloyd, Keith, 2Lott, John R., Jr., 174, 176, 183Lucas, W., 26Lundberg, George A., 29Lundervold, Duane A., 161Lunt, Paul S., 11, 31Lustick, Ian, 69Lynch, Julia, 69Lynd, Helen Merrell, 34, 35, 41–3, 91, 92Lynd, Robert Staughton, 31, 34, 35, 41–3,

91, 92Lynn-Jones, Sean M., 195

MacIntyre, Alasdair, 70MacIntyre, Andrew, 156Mackie, John L., 126, 207Mahon, James E., Jr., 4, 15, 101, 145Mahoney, James, 4, 5, 27, 44, 80, 81, 102,

104, 174, 175, 181, 182

Manski, Charles F., 3Maoz, Zeev, 2, 6, 13Marini, Margaret, 207Marks, Gary, 202Marshall, Monty, 95Martin, Cathie Jo, 47Martin, Lisa L., 47, 78, 145Mayhew, David R., 205Mayo, Deborah G., 117Mays, Nicolas, 2McAdam, Doug, 5, 192McCullagh, Peter, 111McCulloch, Neil, 3McDermott, Rose, 11, 123, 157, 158, 160McKay, Andrew, 3McKeown, Timothy J., 2, 46McNeill, William H., 191McNulty, John E., 158Mead, Melissa, 2Meckstroth, Theodore, 131, 139Meehl, Paul E., 3, 6, 29, 50Meier, Kenneth J., 2Merriam, Sharan B., 2, 19Michels, Roberto, 109, 110Miguel, Edward, 2, 132Mill, John Stuart, 71, 98, 138, 139, 142,

153, 157, 170Miller, Steven E., 195Miron, Jeffrey A., 163Mitchell, J. Clyde, 17Mohr, Lawrence B., 13Monroe, Kristen Renwick, 101Moore, Barrington, Jr., 81, 139, 142Moravsik, Andrew, 191Moreno, Carola, 145, 202Morgan, Stephen L., 3, 11, 134Morrow, James D., 123Most, Benjamin A., 123Moulder, Frances V., 132Munck, Gerardo L., 39, 109

Nagel, Ernest, 131, 142Nelder, J. A., 111Neta, Ram, 70Neuendorf, Kimberly A., 69Nicholson-Crotty, Sean, 2Nissen, Sylke, 2Njolstad, Olav, 54, 120North, Douglass C., 40, 191, 194

Odell, John S., 2, 6, 17Orum, Anthony M., 2, 17, 41–50, 66Ostrom, Elinor, 31

Packwood, Tim, 2Pahre, Robert, 11Palfrey, Thomas R., 157, 160, 162


Name Index 261

Pantaleo, Giuseppe, 105Papyrakis, Elissaios, 48Parker, Ian, 69Patterson, W. David, 164Patton, Michael Quinn, 39, 69, 98Patzelt, Werner J., 164Pavlov, Ivan, 162Phillips, Nelson, 69Phillpot, Robert, 115Pierson, Paul, 75Piore, Michael J., 2Platt, Jennifer, 2, 7, 18Pope, Catherine, 2Popper, Karl, 5, 39, 40–2, 74, 115–17,

118, 120Porter, Michael, 4, 38, 80Posen, Barry, 123Posner, Daniel, 2, 132Poteete, Amy R., 31Pressman, Jeffrey L., 165–8, 169, 174, 178,

179Przeworski, Adam, 3, 26, 27, 50, 79, 95,

131, 139Putnam, Robert D., 27, 156

Queen, Stuart, 17, 30, 91

Rabinow, Paul, 70Ragin, Charles C., 2, 3, 4, 11–13, 17,

41–2, 43, 49, 50, 61, 102, 126, 202Ragsdale, Lynn, 123Reilly, Ben, 75, 101, 115, 120Reiss, Julian, 3Renelt, David, 55Rice, Stuart A., 29Richter, Melvin, 27Ridder, Geert, 134Roberts, Clayton, 173Roberts, Michael J., 10Robinson, Denise L., 2, 19Robinson, James A., 2, 191, 208–10Robinson, W. S., 6, 55Rockman, Bert A., 168Rodgers, Robert, 2Rodrik, Dani, 2, 3, 5Rogowski, Ronald, 54, 104, 120Rohlfing, Ingo, 145Romer, Christina D., 177, 178, 179, 183,

191Rosenbaum, Paul R., 69, 134, 136, 138Ross, Michael, 48, 125–7, 128Roth, Alvin E., 157Rubin, Donald B., 134Rueschemeyer, Dietrich, 4, 27, 41–3, 46,

47, 61Rusk, Jerrold G., 123Russett, Bruce M., 2

Sabin, Lora, 181Sacerdote, Bruce, 48Sala-i-Martin, Xavier X., 3Sarbin, Theodore R., 6Sartori, Giovanni, 15, 37Sayer, R. Andrew, 5Schelling, Thomas C., 123Schmid, Christopher H., 181Schuman, Howard, 157Schwandt, Thomas A., 211Schwartz, Anna Jacobson, 163Schwartz-Shea, Peregrine, 70Scriven, Michael, 173Seawright, Jason, 211Sekhon, Jasjeet S., 6, 115, 145Sengupta, Somini, 166Shadish, William R., 157, 170Shafer, Michael D., 119Shalev, Michael, 52Shapiro, Ian, 81, 82Shelton, Carolyn, 145Shively, W. Philips, 13Shugart, Matthew Soberg, 164Shweder, Richard A., 69Silber, Jeffrey H., 134, 136, 138Silverman, David, 69Simon, Julian Lincoln, 7Singer, Burton, 207Sjoberg, Gideon, 2, 17, 50, 66, 81Skinner, B. F., 162Skocpol, Theda, 22, 75, 80, 81, 102, 131,

139, 142, 174, 175, 178, 179, 181, 182Smelser, Neil J., 6, 27Smith, Alastair, 85Smith, Carolyn D., 69Smitsman, Anneloes, 115Smoke, Richard, 39–43, 46, 51, 75, 76, 78,

80, 99Snidal, Duncan, 6, 31, 39, 46, 145Snyder, Richard, 19, 39Sobel, Michael, 3, 11Somers, Margaret, 75, 81, 131, 139Spence, Lester Kenyatta, 160Srinivasan, T. N., 2Staiger, Douglas, 3Stake, Robert E., 2Stanley, Julian, 17, 29, 41–2, 157Starr, Harvey, 4, 120, 123Steadman, Dawnie Wolfe, 2Stein, Janice Gross, 196Stephens, John D., 41–50, 202Stiglitz, Joseph E., 2Stinchcombe, Arthur L., 115Stock, James H., 3Stoecker, Randy, 2, 17Stoker, Laura, 68, 70Stouffer, Samuel A., 29, 85, 157


262 Name Index

Stratmann, Thomas, 75, 164Strauss, Anselm L., 45Sullivan, William M., 70Summers, Robert, 95Sundquist, James L., 206Swank, Duane H., 47, 100, 202Swedberg, Richard, 5, 44

Tarrow, Sidney G., 5, 173, 192Taylor, Charles, 70, 207Temple, Jonathan, 40, 55Tendler, Judith, 101Tetlock, Philip E., 4, 166, 207Teune, Henry, 3, 27, 50, 79, 131, 139Thacker, Strom, 145, 202Theiss-Morse, Elizabeth, 68Thies, Cameron G., 17, 69Thies, Michael F., 47Thomas, Craig, 40Thomas, Robert PaulThompson, Edward P., 69, 74Tilly, Charles, 5, 44, 192Tooley, Michael, 5Trachtenberg, Marc, 69Treier, Shawn, 95Trow, Martin A., 30, 54, 109, 110, 120Truman, David B., 54, 120Tsai, Lily, 115–19Tsay, Angela, 4, 119Turner, Frederick Jackson, 207

Udry, Christopher, 2, 84Unger, Danny, 115Urbach, Peter, 115–17

Van Evera, Stephen, 2, 17, 115–18Vandenbroucke, Jan P., 2, 40Verba, Sidney, 6, 9, 31, 39, 40, 61, 80, 145,

166, 190Verschuren, Piet J. M., 17Vittinghoff, Eric, 105

Vogt, W. Paul, 211von Wright, Georg Henrik, 70Voss, Kim, 207Vreeland, James Raymond, 2, 75

Wahlke, John C., 146Waller, Willard, 7Wand, Jonathan, 158Wantchekon, Leonard, 158Warner, Andrew, 2Warner, W. Lloyd, 11, 31Watkins, Michael, 2Wattenberg, Martin P., 164Weaver, R. Kent, 168Weber, Max, 207Weingast, Barry R., 40, 78Welsch, Roy E., 110Wildavsky, Aaron, 165–69, 174, 178,

179Wilson, David B., 26Wilson, James Q., 167–68Winch, Peter, 70Winks, Robin W., 69Winner, Hannes, 3, 4, 55Winship, Christopher, 3, 11Winters, L. Alan, 3Wolf, Katherine M., 106Wolin, Sheldon S., 53Wong, Wilson, 13Wood, R. O., 69Woodruff, David M., 70Wundt, Wilhelm, 162

Yanow, Dvora, 70Yashar, Deborah J., 139, 142Yin, Robert K., 2, 17, 75Young, Oran R., 47Young, Pauline, 190

Zeng, Langche, 3Znaniecki, Florian, vi, 3, 50, 55


Subject Index

analytic narrative, 5, 78antecedent cause, 211attribute, 211

bias, 211binary, 122–126, 211breadth, 22, 80, 211

case, 5, 12, 15, 17, 18, 19, 20, 21, 22, 26,27, 29, 30, 37–38, 41, 43, 49, 50, 53,65, 66, 75, 76, 78, 79, 81, 83, 84, 85,86, 88, 91, 93, 94, 96, 97, 100, 101,104, 108, 115–17, 118, 124–7, 131,133, 139, 143, 144, 145, 146, 150, 211

case selection, 71, 98, 99, 101, 115–17,139, 147, 149, see Chapter 5

case study, 1, 5, 6, 7, 8, 12–13, 15, 16, 17,18, 20, 21, 22, 26, 27, 28, 29, 31, 32,33, 34, 36, 37, 38, 39, 40, 41, 42, 43,45, 46, 48, 49, 50, 52, 56–61, 62, 65,66, 68, 73, 74, 75, 76–7, 78, 79, 80, 83,84, 85, 86, 87, 88, 90, 91, 93, 97, 100,121, 122, 126, 130, 138, 139, 142, 143,145, 146, 147, 148, 149, 151–2, 172,173, 174, 211

case-based analysis, 3, 4, 38, 80, 211causal complexity, 4, 21, 38, 61–2, 80causal distance, 212causal effect, 37, 43–8, 55, 66, 134–9, 212causal factor, 21, 41, 212causal inference, 151, 212causal mechanism, 4, 5, 37, 42, 43–8, 55,

212causal order, 212ceteris paribus, 38, 52, 66, 82, 157, 164–8,

171, 212comparative method, 4, 27, 212

comparative-historical analysis, 4, 212confirmatory research, 71, 72, 116–19continuous (scalar) variable, vi, 44, 54,

126–30, 212Cook’s distance, 111, 112, 113–16, 158,

170correlation, 212Counterfactual Comparison, 152, 154,

165–8, 169, 182, 197, 206, 212counterfactual thought experiment, 4,

212covariation, 27–9, 30, 41, 44, 73, 213critical juncture/path dependence, 213cross-case study, 1, 7, 10, 12–13, 16, 20,

21, 22, 26, 27, 29, 30, 31, 34, 35, 36,37–9, 40, 41, 42, 43, 44, 46, 48, 49, 50,51, 52, 53, 54, 56–60, 61, 62, 66, 75,77, 78, 84, 85, 88, 90, 91, 93–6,99–100, 102–3, 104, 106–14, 121, 122,126–30, 134–8, 139, 141, 146, 147,148, 172, 173, 213

cross-sectional, 3, 21, 28, 32, 77, 213crucial case, 88, 115–17, 118, 119,

120–21, 147, 213

dependent variable, 6, 21, 28, 71, 101,104, 110, 111, 113, 135, 136, 213

descriptive inference, 213deterministic, 54, 126–30, 213deviant case, 88, 105–7, 108, 110, 146,

147, 153, 213diachronic, 21, 27, 213dichotomous scale, 213distal cause, 213diverse case, 88, 90, 97–9, 101, 144, 147,

213domain, 213

263


264 Subject Index

Dynamic Comparison, 152–4, 157,164–168, 197, 204, 213

econometrics, 3endogenous cause, 213equifinality, 213ethnography, 17, 18, 213exogenous cause, 213experimental research design, 11–12, 213experimental template, 214exploratory research, 153external validity, 37, 43–50, 102, 214extreme case, 88, 90, 101–2, 104, 147,

153, 214

falsifiability, 74–75, 214field research, 214

hat matrix, 110–11hermeneutics, 214hypothesis, 6, 22, 38, 39–43, 71–4, 76, 78,

79, 82, 84, 92, 93, 99, 114–16, 131,148, 149, 192, 214

hypothesis-generating studies, 39–43, 72,80, 116–119

hypothesis-testing studies, 39–43, 72

independent variable, 6, 21, 28, 41, 71, 93,99, 101, 112, 113, 135, 136, 137, 139,149, 214

inference, 22, 81, 82, 83, 84, 85, 90, 214influential case, 3, 88, 108–110, 114–16,

147, 214intermediate cause, 214internal validity, 37, 43–50, 67, 151–2,

172–173, 214interpretivism, 69, 71, 214intervention, 214

K, 52, 93, 214

large-N study, 5, 10, 21, 33, 35, 36, 37, 44,45, 51, 54, 65, 88, 91, 93, 94, 99, 100,107, 121, 124–6, 127, 137, 138, 139,141, 142, 172, 183, 214

least-likely case, 115–18, 119, 214level of analysis, 214level of measurement, 215Longitudinal Comparison, 152–4, 156,

160–68, 169, 171, 197, 205, 215

matching procedure, 134–7meta-analysis, 26method of difference, 215minimal-rewrite rule, 215most-different cases, 31, 139–42, 144, 147,

215

most-similar cases, 88, 131, 136, 137, 138,139, 144, 147, 189, 203–4, 215

N, 20, 29–33, 52, 112, 114–16, 180, 183,215

natural experiment, 215naturalistic, 17, 18, 215necessary cause, 215nested analysis, 153, 189, 198–203, 215nominal scale, 99, 215

observation, 20, 26, 29, 30, 32, 52, 67, 68,215

observational research design, 11–12, 215operationalization, 215optimal sequence matching, 4ordinal scale, 99, 215

participant observation, 17, 215path dependence, 3, 75, 215pathway case, 88, 122, 124–7, 130, 131,

147, 216population, 20, 21, 22, 26, 37–8, 41, 43,

44, 52, 66, 69, 80, 81, 82, 83, 84, 85,86, 87, 88, 90, 91, 93, 104, 147, 216

positivism, 5probabilistic, 216process tracing, 15, 17, 18, 173, 178–84,

185, 216proposition, 22, 82, 216proximal (proximate) cause, 216

qualitative, 9, 10–11, 17, 18, 29, 33, 35,36, 68, 91, 138, 139, 180, 183, 216

Qualitative Comparative Analysis (QCA),4, 9, 99, 126–8, 216

quantitative, 9, 10–11, 29, 33, 36, 68, 90,134, 179, 183, 216

quasi-experiment, 216

randomization, 87, 216rational choice, 5realism, 5representativeness, 92, 96, 216research design, 18, 184, 216

sample, 20, 21, 22, 35, 83, 86, 87, 93, 100,102, 144, 145, 147, 216

scope, 217selection bias, 217single-outcome study, 8, 187–210, 217singular observations, 8, 17, 18, 19, 20,

21, 188, 217small-N study, 17, 18, 33, 65, 87, 91, 94,

100, 124–7, 130, 141, 217Spatial Comparison, 151–2, 154, 156,

164–5, 168–9, 197, 204, 217


Subject Index 265

stochastic, 97, 113–16, 217structural cause, 217sufficient cause, 217synchronic, 21, 27, 217

triangulation, 17, 18, 217typical case, 88, 90, 91, 93, 96, 106, 147,

153, 217typological theorizing, 98

unit, 217unit homogeneity, 217unit of analysis, 217

validity, 43–50, 217variable, 3, 41, 44, 52, 68, 86, 91, 93,

97, 98, 99, 102, 107, 108, 113, 122,126–8, 130, 132, 133, 135, 136, 143,148, 217

Verstehen, 19, 37, 217

within-case analysis, 11, 18, 19, 21, 27, 28,30, 31, 32, 33, 35, 36, 44, 51, 84, 85,96, 189, 204–7, 217

X (see also independent variable), 42, 43,44, 45, 50, 56–61, 71, 72, 73, 75, 99,102, 104, 105, 111, 112, 143, 148,164–8, 169, 171, 179, 217

X-centered analysis, 54, 71, 72, 217X1/Y– centered analysis, 54, 55, 56–60,

71, 72, 193, 218

Y (see also dependent variable), 42, 43, 44,45, 50, 54, 55, 56–61, 71, 72, 73, 75,92, 93, 98, 99, 101, 104, 105, 107, 111,122–6, 127, 128, 130, 138, 139, 143,144, 147, 148, 151, 152, 154, 164–8,169, 170, 172, 173, 179, 180, 182, 183,184, 218

Y-centered analysis, 71, 218

Case Study Research: Principles and Practices

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